Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

The integration of single-cell datasets across species is a powerful approach to understanding how cell types and patterns of gene expression have evolved. Current methods to perform such integrations require multiple steps: clustering, the integration itself, and downstream differential expression analysis. In this study, the authors describe a new approach, called ANTIPODE, that combines these steps by integrating deep learning with interpretable decoding and linear modeling. This method builds on previous deep learning approaches to dataset integration, namely SCVI and scANVI, that employ a variational autoencoder to model single-cell RNA-sequencing datasets. However, gene expression estimates from these previous methods are challenging to interpret due to non-linear decoding from the modeled latent space. ANTIPODE seeks to address this issue by using a single-layer decoder coupled to a linear model to estimate patterns of differential expression, e.g. differential expression by coexpression module, across cell types, etc.

The authors apply their framework to a large single-cell RNA-seq dataset (~1.8M cells) containing cells from the central nervous systems of humans, macaques, and mice spanning in utero developmental time points. They identify a consensus set of cell clusters across each species. They find that ANTIPODE performs at least as well as SCVI in terms of species integration and batch correction. The authors demonstrate several use cases of this integrated approach by analyzing differential expression that correlates with gene structure, the evolution of expression differences in neuropeptide systems, and the anatomical and phylogenetic variation in neurodevelopmental timing.

Strengths:

ANTIPODE is a welcome addition to techniques that integrate large single-cell RNA-seq datasets across multiple species. The approach's simultaneous inference of cell clusters, integration manifolds, and differential expression should streamline analysis pipelines whose elements are often disjointed and sometimes work at cross purposes.

Weaknesses:

The authors note several limitations to their method that will be targets for future development. First, clustering "resolution" is inferred from the data and cannot be tuned as with other approaches. Second, because of the linear decoding, ANTIPODE does not accommodate combining datasets obtained from different modalities (e.g. single-cell with single-nucleus RNA-seq). Third, as currently implemented, ANTIPODE does not explicitly model phylogenetic relationships. However, the authors describe an extension that could enable this, enhancing the power of multiple species integrations. A weakness with the current manuscript is the organization and readability of the figures. The supplemental figures in particular need to be restructured and reformatted to increase their interpretability.

We thank this reviewer for their positive feedback regarding the utility of the model and how it may simplify challenging evolutionary analysis.

We acknowledge that the figures are a bit difficult to read, and we will improve annotation and tidiness to make them more accessible to the reader.

We have implemented changes for an ANTIPODE version 0.2 version which includes regression of gene expression differences on a phylogeny. We have updated the github with this “antipode.phylo” module. For this study, the 3 species case is equivalent for flat or phylogenetic regression, where for example mouse up is equivalent to primate down, so we will do not plan to redo the analyses in the text using this new version.

We have already provided examples for running ANTIPODE on our own and public datasets (https://github.com/mtvector/scANTIPODE/tree/main/real_examples), as well as in-line documentation of classes and functions, however it is true that these may be insufficient information for new users. We will provide true explanatory tutorials for both to address the reviewer’s concerns. ANTIPODE version 0.1 is currently installable from either github or PyPI.

Reviewer #2 (Public review):

Summary:

This work presents ANTIPODE, a bilinear generative model developed for the simultaneous integration and identification of cell types across species and developmental stages using single-cell RNA-seq data. ANTIPODE is inspired by scANVI, a well-established semi-supervised framework for single-cell transcriptomics. After describing its implementation, the authors use ANTIPODE to integrate data from 15 species comprising 1,854,767 cells. Then, the authors benchmark ANTIPODE against commonly used methods (scVI, Harmony, and Scanorama) using two snRNAseq datasets and report comparable or superior performance. They then return to the initial integrated dataset and analyse patterns of gene expression evolution. Finally, they leverage the model to study the "later-is-larger" concept, evaluating the relationship between gene expression, developmental timing and structure size and finding gene expression signatures of this concept.

Strengths:

A major strength of the paper is that ANTIPODE employs a bilinear decoding architecture, which produces more interpretable model parameters while performing at least as well as existing, more opaque nonlinear integration approaches.

The authors demonstrate the utility of ANTIPODE by integrating single-cell mRNA sequencing data from mouse, macaque, and human brains and confirming general principles regarding developmental timing and cell-type-specific gene expression divergence.

They also propose a conceptually interesting framework for studying gene expression evolution: instead of focusing solely on differentially expressed genes between homologous cell types, they jointly model gene expression across developmental states and species-specific divergence, allowing them to define and analyse four categories of differential expression.

Finally, the authors' conclusions are well supported by the analyses presented, although these conclusions remain relatively conservative and reinforce already established principles.

Weaknesses:

A central weakness of the paper is its limited accessibility to a broad audience. Despite attempting to keep computational details in the supplement, the main text still uses substantial jargon, undermining the goal of providing an intuitive explanation of the model. The figures are also insufficiently annotated (e.g., colour schemes in Figure 2 heatmap, bubble plot details in Figure 3, entropy definition in Figure 3), and the figure legends are overly brief and lack essential information. I strongly recommend that the authors revise both text and figures to improve clarity and readability.

Similarly, the materials and methods lack a lot of information about the implementation of the model, the statistical tests used, the calculations of entropy, etc.

The study sits between tool development and biological discovery but does not fully commit to either. As a result, it cannot be evaluated as a full benchmarking study, yet it also does not provide new biological insights that are validated experimentally.

Finally, the GitHub repository for ANTIPODE is not yet functional and lacks documentation or tutorials, making it impossible to assess usability or reproducibility.

Author response:

We would like to thank the Editor and the three Reviewers for their detailed assessment of our manuscript and their constructive feedback. We found the suggestions valuable for refining our work. Before presenting the fully updated manuscript, we would like to clarify a few points in this initial response. This manuscript identifies a heat-induced, alternativelyspliced short isoform of PIF4 (PIF4-S) that contributes to the physiological responses observed in heat-stressed etiolated seedlings. First, we agree with all Reviewers that including PIF4 protein data will strengthen our findings an more definitely demonstrate the generation of a protein-coding alternative isoform under heat stress. Therefore, this will be one of our main priorities in the revision. Evidence for the functionality of this alternative isoform is clearly demonstrated by the distinct phenotypes exhibited by transgenic lines expressing either the long or the short versions of PIF4. Nevertheless, we agree that a more comprehensive characterization of these lines, as well as of the pif4 mutant lines, will further strengthen the demonstration of the functional relevance of this alternative splicing event. In addition, we will extend the phenotypic analysis of the PIF4-S lines to heat stress conditions. Importantly, the phenotypes observed in these lines suggest that additional molecular mechanisms may act in parallel with this alternative splicing event to regulate development in heat-stressed etiolated seedlings. As proposed by Reviewer #1, other PIFs may be involved in this response, and we will address this possibility. We will also provide new experimental data to show that alternative splicing in this gene is specific to heat stress and does not occur in other PIFs. Finally, we would like to clarify that the main scope of this manuscript is to demonstrate the functional relevance of the alternative isoform generated by splicing in PIF4 under heat stress. A detailed investigation of its molecular mode of action is beyond the scope of the present study. We sincerely appreciate the thoughtful feedback provided by all Reviewers. We will carefully consider their suggestions and use them to guide the inclusion of additional experiments and analyses in our revised manuscript to reinforce and clarify our conclusions.

Author response:

The following is the authors’ response to the original reviews

eLife Assessment

The manuscript by Shukla et al. provides important mechanistic insights into kinesin-1 autoinhibition and cargo-mediated activation. Using a convincing combination of protein engineering, computational modeling, biophysical assays, HDX-MS, and electron microscopy, the authors reveal how cargo binding induces an allosteric transition that propagates to the motor domains and enhances MAP7 binding. Despite limitations arising from conformational heterogeneity and structural resolution, the study presents a unified mechanism for kinesin-1 activation that will be of broad interest to the motor protein, structural biology, and cell biology communities.

We are grateful for the time and effort from the reviewers and editors in providing fair and constructive comments that have helped to improve the manuscript. Our point-by-point response is provided below.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors aim to interrogate the sets of intramolecular interactions that cause kinesin-1 hetero-tetramer autoinhibition and the mechanism by which cargo interactions via the light chain tetratricopeptide repeat domains can initiate motor activation. The molecular mechanisms of kinesin regulation remain an important question with respect to intracellular transport. It has implications for the accuracy and efficiency of motor transport by different motor families, for example, the direction of cargos towards one or other microtubules.

Strengths:

The authors focus on the response of inactivated kinesin-1 to peptides found in cargos and the cascade of conformational changes that occur. They also test the effects of the known activator of kinesin-1 - MAP7 - in the context of their model. The study benefits from multiple complementary methods - structural prediction using AlphaFold3, 2D and 3D analysis of (mainly negative stain) TEM images of several engineered kinesin constructs, biophysical characterisation of the complexes, peptide design, hydrogen/deuterium-exchange mass spectrometry, and simple cell-based imaging. Each set of experiments is thoughtfully designed, and the intrinsic limitations of each method are offset by other approaches such that the assembled data convincingly support the authors' conclusions. This study benefits from prior work by the authors on this system and the tools and constructs they previously accrued, as well as from other recent contributions to the field.

Weaknesses:

It is not always straightforward to follow the design logic of a particular set of experiments, with the result that the internal consistency of the data appears unconvincing in places.

For example, i) the Figure 1 AlphaFold3 models do not include motor domains whereas the nearly all of the rest of the data involve constructs with the motor domains;

We appreciate the reviewer’s comment regarding the absence of the motor domains in the AlphaFold3 models shown in Figure 1. These domains were intentionally excluded to improve visual clarity and to better highlight the interaction between the TPR domains and CC1 in the inhibited kinesin-1 conformation. We felt that this simplified presentation in the main figure helps readers focus on the key mechanistic advance introduced in this work at the outset of the paper. For completeness, we have provided full-length kinesin-1 AlphaFold3 models that include the motor domains in the Supplementary Information (Fig. S1), and they are described in detail in the main text. In addition, we have added a note to the Figure 1 legend to explicitly direct readers to these full-length models.

ii) the kinesin constructs are chemically cross-linked prior to TEM sample preparation - this is clear in the Methods but should be included in the Results text, together with some discussion of how this might influence consistency with other methods where crosslinking was not used.

Thank you. Chemical crosslinking is typically important for obtaining high-quality negative-stain TEM grids of kinesin-1 complexes and has been employed in all prior EM studies by our group and others. While this was described in the Methods, we agree that it should also be stated explicitly in the Results. Accordingly, we have added a sentence to the Results section noting that the proteins were stabilized using the amine-to-amine crosslinker BS3 (“Proteins were also stabilised using the amine-to-amine crosslinker BS3 that was important for achieving reproducibly high-quality samples for imaging.”).

Please see point below for acknowledgement of risks of using crosslinker.

Can those cross-links themselves be used to probe the intramolecular interactions in the molecular populations by mass spec?

We had considered this, however, cross-linking mass spectrometry (XL-MS) has been applied extensively to essentially identical kinesin-1 complexes by Tan et al. (eLife 2023). That work provided important insights into the overall architecture of the complex, including the new head–CC1 interactions. However, as fully acknowledged by the authors, significant ambiguity remained with respect to the positioning of the TPR domains, with many cross-links that could not be straightforwardly rationalized in a single model. These unresolved aspects provided part of the motivation for the present study, as highlighted in the Introduction.

We believe that this ambiguity likely reflects an underlying conformational equilibrium of the kinesin-1 complex (e.g. opening/closing transitions) and/or dynamic docking and undocking of the TPR domains, and lysine-rich features of the TPR domains (most notably the loops that connect the TPR alpha helices) which may make them prone to lock in non-native states, which limits the interpretability of static cross-linking data in this system. In this context therefore, we feel that XL-MS has already been thoroughly explored for kinesin-1 and that its practical limitations in resolving these TPR interactions have been reached.

This consideration was a primary motivation for pursuing cross-linker-free, solution-based approaches, particularly HDX-MS, which we argue provide the most relevant new insights into the assembly and conformational dynamics of the complex. To make this rationale clearer, we have added an explicit note in the HDX-MS section emphasizing that this is a cross-linker-free method. The added text reads:

“To determine how the local structural changes from adaptor binding and shoulder dislocation affected the dynamics of kinesin-1 complexes in solution, as directly and least invasively as possible, and without the risk of cross-linker artefacts.”

In general, the information content of some of the figure panels can also be improved with more annotations (e.g. angular relationship between views in Figure 1B, approximate interpretations of the various blobs in Fig 3F, and more thought given to what the reader should extract from the representative micrographs in several figures - inclusion of the raw data is welcome but extraction and magnification of exemplar particles (as is done more effectively in Fig S5) could convey more useful information elsewhere.

We appreciate these suggestions. We have modified the figures throughout the manuscript in line with the reviewer’s points. Raw data is now provided at higher magnification throughout so the reader can better distinguish individual particles, angular relationships have been added and further annotations provided on 2D class averages. We do not want the reader to draw too many conclusions from images of single closed particles (with the exception of open vs closed in Fig S7) as these require averaging and 2D classification to obtain meaningful insights, and so we have not added zoom panels in these cases. Figure 3F has been annotated as requested.

Reviewer #2 (Public review):

Summary:

In this paper, Shukla, Cross, Kish, and colleagues investigate how binding of a cargo-adaptor mimic (KinTag) to the TPR domains of the kinesin-1 light chain, or disruption of the TPR docking site (TDS) on the kinesin-1 heavy chain, triggers release of the TPR domains from the holoenzyme. This dislocation provides a plausible mechanism for transition out of the autoinhibited lambda-particle toward the open and active conformation of kinesin-1. Using a combination of negative-stain electron microscopy, AlphaFold modeling, biochemical assays, hydrogen-deuterium exchange mass spectrometry (HDX-MS), and other methods, the authors show how TPR undocking propagates conformational changes through the coiled-coil stalk to the motor domains, increasing their mobility and enhancing interactions with the microtubule-bound cofactor MAP7. Together, they propose a model in which the TDS on CC1 of the heavy chain forms a "shoulder" in the compact, autoinhibited state. Cargo-adaptor binding, mimicked here by KinTag, dislodges this shoulder, liberating the motor domains and promoting MAP7 association, driving kinesin-1 activation.

Strengths:

Throughout the study, the authors use a clever construct design - e.g., delta-Elbow, ElbowLock, CC-Di, and the high-affinity KinTag - to test specific mechanisms by directly perturbing structural contacts or affecting interactions. The proposed mechanism of releasing autoinhibition via adaptor-induced TPR undocking is also interrogated with a number of complementary techniques that converge on a convincing model for activation that can be further tested in future studies. The paper is well-written and easy to follow, though some more attention to figure labels and legends would improve the manuscript (detailed in recommendations for the authors).

Weaknesses:

These reflect limits of what the current data can establish rather than flaws in execution. It remains to be tested if the open state of kinesin-1 initiated by TPR undocking is indeed an active state of kinesin-1 capable of processive movement and/or cargo transport. It also remains to be determined what the mechanism of motor domain undocking from the autoinhibited conformation is, and perhaps this could have been explored more here. The authors have shown by HDX-MS that the motor domains become more mobile on KinTag binding, but perhaps molecular dynamics would also be useful for modelling how that might occur.

We are grateful for the reviewer’s comments. We agree that the weaknesses the reviewer has outlined define the limitations of the study and establish important priorities for future work, that includes molecular dynamics simulations. An important prerequisite for the latter is a starting model that one has confidence in. We think that our study and earlier work now provide a good experimentally supported foundation for using AF3 generated assemblies for this purpose, by ourselves and others.

Reviewer #3 (Public review):

Summary:

The manuscript by Shukla and colleagues presents a comprehensive study that addresses a central question in kinesin-1 regulation - how cargo binding to the kinesin light chain (KLC) tetratricopeptide repeat (TPR) domains triggers activation of full-length kinesin-1 (KHC). The authors combine AlphaFold3 modeling, biophysical analysis (fluorescence polarization, hydrogen-deuterium exchange), and electron microscopy to derive a mechanistic model in which the KLC-TPR domains dock onto coiled-coil 1 (CC1) of the KHC to form the "TPR shoulder," stabilizing the autoinhibited (λ-particle) conformation. Binding of a W/Y-acidic cargo motif (KinTag) or deletion of the CC1 docking site (TDS) dislocates this shoulder, liberating the motor domains and enhancing accessibility to cofactors such as MAP7. The results link cargo recognition to allosteric structural transitions and present a unified model of kinesin-1 activation.

Strengths:

(1) The study addresses a fundamental and long-standing question in kinesin-1 regulation using a multidisciplinary approach that combines structural modeling, quantitative biophysics, and electron microscopy.

(2) The mechanistic model linking cargo-induced dislocation of the TPR shoulder to activation of the motor complex is well supported by both structural and biochemical evidence.

(3) The authors employ elegant protein-engineering strategies (e.g., ElbowLock and ΔTDS constructs) that enable direct testing of model predictions, providing clear mechanistic insight rather than purely correlative data.

(4) The data are internally consistent and align well with previous studies on kinesin-1 regulation and MAP7-mediated activation, strengthening the overall conclusion.

Weaknesses:

(1) While the EM and HDX-MS analyses are informative, the conformational heterogeneity of the complex limits structural resolution, making some aspects of the model (e.g., stoichiometry or symmetry of TPR docking) indirect rather than directly visualized.

We agree with the reviewers point. Conformational heterogeneity is a significant challenge, and the model has been developed from multiple complementary approaches. A higher resolution cryoEM study remains a priority, but is challenging because of the size, shape and flexibility of the particle, but we hope that some the approaches used here (e.g. nanobody TPR stabilisation, ElbowLock) will provide a path to achieve this.

(2) The dynamics of KLC-TPR docking and undocking remain incompletely defined; it is unclear whether both TPR domains engage CC1 simultaneously or in an alternating fashion.

We agree that this is a limitation. We strongly suspect that the TPR domains dynamic and are working to overcome experimental challenges to resolve this important outstanding question. We have expanded the discussion section to better highlight this important priority.

(3) The interplay between cargo adaptors and MAP7 is discussed but not experimentally explored, leaving open questions about the sequence and exclusivity of their interactions with CC1.

We agree that this is a limitation but will be an important priority for future studies.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

There are a number of places where the text could be more precise or clear, or the figures could be designed to be more informative:

(1) The word "unitarily" is used in several places, and I don't know what it means in this context.

We have changed the phrasing throughout the manuscript to this term. We were attempting to contrast with presumed cooperative multivalent interactions in the context of the kinesin-1 tetramer but agree that this choice of word doesn’t quite achieve that.

(2) On page 5 the phrase "We focused on the ElbowLock background" is introduced and needs to be explained more clearly.

Thank you. We have amended the text to read “This KIF5C construct contains a short 5 amino acid deletion that restricts flexibility around the elbow and helps maintain particles in their lambda conformation, providing homogenous samples, and facilitating subsequent analysis (34).”

(3) On page 6, the phrase "To improve the resolution of our images, we turned to single-particle cryoEM analysis" is imprecise - what do the authors mean by the resolution of the images? Cryo-EM data does not always guarantee a higher resolution structure, but it offers the possibility of visualising finer structural features. This is probably what is meant here, but needs to be stated more precisely.

We have amended the text to ‘visualise finer structural details’ as suggested.

(4) Page 7 - "suggesting that TPR domains had loosely dissociated from the core" - I don't think the evidence points to dissociation of KLCs from the complex, but the phrase "loosely dissociated" implies this - would benefit from rephrasing.

We have changed this to ‘undocked’ for consistency with other descriptions in the manuscript.

(5) Was the effect of the CC-Di insertion (ΔTDS) detectable by AlphaFold prediction? It would be interesting to include this, partly for completeness and partly because a slightly imperfect and maybe a more dynamic coiled-coil in this region of the molecule may be important in supporting the conformational changes required for activation.

Thank you for this suggestion. Modelling of deltaTDS complex indeed shows displacement of the TPR domains. In the standard 5 output models, the TPR domains now occupy a variety of different positions, all with essentially zero confidence (high position error). Consistent with biochemical data, the CCDi insertion is modelled with with no overall disruption to the architecture or length of CC1 as expected. We think that this is a valuable addition to the study and have included it as a new supplementary figure (Fig S5), with main text reading.

…. “Supporting this, models of ΔTDS complexes using AF3 showed the expected seamless insertion of CCDi into CC1, with displacement of the TPR domains to a variety of different positions, in 5 models, all with high position error with respect to KHC (Fig S5).”

(6) Figure S1 has two sections designated (C) in the legend.

Corrected

(7) Figure S3 - given the resolution and level of interpretation of the 3D reconstructions, it is not relevant to include an FSC curve, but other standard information, such as angular distribution and any evidence of variability from 3D classifications (and how many particles per 3D class) should be included for all structures.

Thank you, a complete workflow for all complexes has now been provided in Figure S8 with the information requested. In each case there were typically two ‘good’ classes. For ElbowLock, this included one without a prominent shoulder, consistent with 2D classification and quantification. We assume this may reflect a docking/undocking equilibrium. For the deltaTDS and KinTag particles, neither class showed the shoulder feature. The main text has been modified to reflect this and reads “For ElbowLock complexes, this resulted in classes with and without a prominent shoulder, in agreement with 2D classification. For ElbowLock-ΔTDS and ElbowLock-KinTag complexes, no prominent shoulder containing classes were observed.”

Reviewer #2 (Recommendations for the authors):

Overall, the figures would benefit from more labels for clarity, some examples and suggestions below:

(1) Figure 1A - Connect motors to the rest of the structure e.g., wiggly lines.

Corrected.

(2) Figure 1B - Add arrows and angles to indicate different views of the model.

Corrected.

(3) Figure 1B - Label TPR1-6 (e.g., inset zoom in).

Corrected.

(4) Figure 2D and 3D - Label the lack of a shoulder in all averages (perhaps with an arrow instead of a circle to not obscure density), include an example average which shows prominent shoulder density.

Corrected. Full sets of classes showing shoulder like features for deltaTDS and KinTag complexes are now shown in Figure S4.

(5) Figure 3D: Label motor domains and elbow as in other figures.

Corrected.

(6) Methods: Include more information on how EM classes were compared to AF projections (e.g., Figure 1D). Was this done visually or computationally? Likewise, more information is needed on how classes were judged to have prominent/weak shoulder density (Figure 2D). In the figure legend, there is a statement that "Full sets of classes are provided in Fig. S4" but this is absent in the supplement.

Thank you. This information has been added to the methods.

“For comparison to the AF3 model, simulated density was generated using the molmap command in ChimeraX (73) filtering to 15 Å, and projections were generated/selected automatically using the Reference Based Auto Selected 2D function in CryoSPARC”.

Full sets of classes are now provided in Figure S4.

(7) Figure 1-3 - Raw micrographs are a very useful inclusion but would benefit from being a more zoomed-in view (e.g., Figure S5 scale). Particularly useful for 3C, where the mixture of open and closed would be good to see.

Higher zoom micrographs have been provided throughout.

(8) Figure 5D: Panels too small to see the result, suggest making full width and moving E below.

Thank you. We have expanded the panel and moved the model to a new Figure 6.

(9) Figure S1: PAE plot convincing, but pLDDT colour models needed.

A representative model coloured for pLDDT has been added to Figure S1. Most of the structure sits within the light blue confident range (90 > pLDDT > 70) with the exception of the disordered regions and neck coil.

(10) Figure 5B: Reason for the variable inputs?

The reviewer raises an interesting point. The slightly reduced expression of deltaElbow and slightly increased expression of ElbowLock is a consistent feature of these experiments. We note that this effect is in the ‘opposite direction’ to the impact on binding to MAP7 and so does not affect our conclusions from the experiment. However, we wonder whether opening and closing of the complex may impact on turnover of kinesin proteins, which could have implications for their normal homeostasis and possible degradation after transport in polarised cells. We are considering how to explore this going forwards. We have added a note to the results section to highlight this interesting observation to the reader.

“We also noted slightly elevated expression of ElbowLock complexes and slightly lower expression of DeltaElbow complexes, suggesting that opening/closing of the complex could impact on kinesin-1 turnover”

(11) Figure legend 5B: Insufficient detail, the end result is stated, but the three separate gels are not described.

Legend has been expanded.

(12) Figure 3F: Currently somewhat problematic. It is unclear if the models are in the same view, and so comparison is difficult. Figure 1C (bottom right) shows class averages with a clear, separate CC density, so the relatively featureless model in this region is puzzling. A statement on how the three model views are related to each other, if aligned with each other, would be useful.

We appreciate the reviewers point. Models were aligned in Chimera, using the fit in map command. Because of the limited features of the models presumably due to flexibility, achieving a good alignment for all three models was challenging, but we think that showing the 180-degree rotations is probably about the best we can achieve here.

(13) The following statement is too strong: "Nonetheless, we obtained reference-free 2D class averages that appeared to show full-length 'side' views of the complex with clear definition of the elbow, hinge 2, and KHC-KLC (coiled-coil) interface features which enabled us to identify CC1 confidently (Fig. 1D)". Given that the negative-stain EM data were collected primarily to validate the AlphaFold model, the assignment of CC1 should be described as consistent with rather than confidently identified from the class averages. The resolution of the EM data does not independently support such an assignment, and the wording needs to be softened.

We appreciate the reviewer’s point, we have softened the wording as suggested. The paragraph now reads.

“To visualise finer structural details, we turned to single-particle cryoEM analysis of frozen-hydrated samples. We were unable to obtain optimal samples suitable for determining the complete structure. Nonetheless, we obtained reference-free 2D class averages that appeared to show full-length ‘side’ views of the complex with clear definition of the elbow, hinge 2, and KHC-KLC (coiled-coil) interface features (Fig. 1D). The motor domains were poorly resolved in these classes, suggesting that the head assembly is somewhat flexible relative to the coiled coil/TPR body. A comparison to low-pass filtered back-projections from the AF3 model (without motor domains) revealed density at a position concurrent with the docked TPR domains (Fig. 1D).”

(14) There is a typo in the figure legend of Figure 3 - (E) and (F) should be (F) and (G).

Corrected

Reviewer #3 (Recommendations for the authors):

I recommend the following additions:

(1) Figure 1 labeling - In panel A, please label the "linker domain" and the "KLC subunits" explicitly to help orient the reader. In panel B, please mark the "TPR shoulder" corresponding to the docked TPR domains on CC1; this will help the reader connect parts B and C.

Thank you, we have modified Figure 1A with this additional information.

(2) The TPR docking site (TDS) is a central structural element, and its sequence boundaries are provided in the Methods. It would help to visualize this directly in Figure 2A or in an inset.

We hope that the reviewer agrees that the zoomed in model in Figure 5A (alongside MAP7) provides a sufficiently detailed view of the structural interface to highlight the orientation of TPR1 with respect to CC1. The side chain contacts in the model are very plausible and confidently predicted (and can be straightforwardly reproduced in AF3 using the sequence information provided in the methods), but as our study has not explored this interaction at the single residue level, we would prefer not to imply this to the reader at this stage.

(3) The authors' model of cargo-induced TPR dislocation is convincing. However, the Discussion could benefit from a clarification on whether both KLC-TPR domains are expected to be bound simultaneously or if a dynamic exchange occurs, as the EM data suggest potential asymmetry.

Thank you, please see point 5 below where we have modified the discussion to reflect the reviewer’s thoughtful comments.

(4) The HDX-MS analysis is comprehensive, but the authors may want to briefly comment on the coverage of low-signal regions (especially within CC2-CC3) to enhance clarity.

We have added an additional supplementary figure (S10) showing sequence coverage. Overall, this is 88% but with some lower coverage around KHC-CC0 (neck) and the acidic linker that connects the KLC coiled-coil to the TPR. We have added a note to the main text to reflect this.

“Sequence coverage was high (overall 88%) with the exception of KHC-CC0 (neck coil) and the acidic-linker region that connects the KLC coiled-coil to the TPR domains where coverage was lower”

(5) In the Discussion, the proposed interplay between MAP7 and cargo adaptors is intriguing, especially considering the results from Anna Akhmanova's lab showing that MAP7 activates kinesin-1 processivity. Do the authors suggest that competition for CC1 is mutually exclusive or sequential? The answer has mechanistic implications.

We have been considering questions for some time, and the short answer is that we don’t fully understand the dynamics yet. However, we appreciate the reviewer’s prompt to clarify our thinking on this. We have attempted to do this in a revised discussion section where we more explicitly outline these outstanding questions.

Author response:

eLife Assessment

This manuscript provides an important contribution to the field of platelet biogenesis, and the convincing evidence will advance our understanding of signal transduction driving the development of late megakaryopoiesis and platelet reactivity that results in bleeding diathesis. The paper is noteworthy for analyzing two related, either singly or in combination, tyrosine phosphatases in this conditional, stage development gene knockout. Because SHP1 is a negative regulator and SHP2 is an activator, the synergistic effects found in the double knockout were surprising.

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

Public Reviews:

Reviewer #1 (Public review):

Barré et al. investigated the role of Shp1 and Shp2 in megakaryocytes (MKs) and platelets by conditional knock-out of Shp1, Shp2, or both under the control of the Gp1ba promoter. Deletion of Shp1 and Shp2 in MKs and platelets was almost complete. The Shp1/Shp2 double knock-out mice displayed macrothrombocytopenia and increased bleeding, whereas the single knock-outs did not show significant defects. Platelet function was aberrant in DKOs, but not in single knock-outs, and so was ligand-induced signaling, particularly Syk phosphorylation.

Megakaryocyte maturation was impaired in Shp1/Shp2 DKO mice. Ligand-induced signaling was impaired in Shp2 knock-out and DKO. Ex vivo formation of platelets and in vivo maturation of MKs were impaired in DKO mice. Pharmacological inhibitors of Shp1 and Shp2 had largely similar effects as observed in the single knock-outs. The authors conclude that Shp1 and Shp2 have synergistic functions in the MK/platelet lineage, and that Shp2 may be a potential therapeutic target in myeloproliferative neoplasms.

Strengths:

The data clearly show effects of the Shp1/Shp2 double knock-out on MKs and platelets.

Weaknesses:

There appears to be a discrepancy between the results with the Shp2 single knock-out and the Shp2 inhibitor: the Shp2 knock-out does not affect MKs and platelets, except Erk1/2 signaling, whereas the Shp2 inhibitors appear to affect MK function.

This work is interesting and may have potential from a therapeutic point of view.

Pharmacological effects do not always correlate with congenital anomalies arising for genetic defects. The Shp2 allosteric inhibitors used in our study only inhibit catalytically inactive Shp2, whereas targeted deletion of Ptpn11 results in a loss of total Shp2 expression, including catalytic and non-catalytic related functions, with developmental consequences. Further, Gp1ba-Cre+;Shp2fl/fl megakaryocytes express approximately 22% of normal Shp2 level, which likely also contributes to differences observed between pharmacological inhibition and genetic ablation of Shp2.

We thank the reviewer for recognizing the therapeutic potential of our findings.

Reviewer #2 (Public review):

Summary:

In this manuscript, Barré et al. investigate the roles of the phosphatases Shp1 and Shp2 in the megakaryocyte and platelet lineage using genetic depletion in mice. By employing Gp1ba-Cre-based models, the study builds on the authors' previous work and addresses some limitations associated with earlier Pf4-Cre approaches. The authors report relatively mild alterations in megakaryocyte and platelet parameters in mice lacking either Shp1 or Shp2 alone, whereas combined deletion of both phosphatases results in macrothrombocytopenia, mild bleeding, and impaired GPVI-dependent platelet aggregation accompanied by reduced Syk phosphorylation. The functional platelet defects are linked to reduced expression of GPVI and integrin α2, while thrombocytopenia is associated with impaired megakaryocyte maturation, reduced ploidy, defective proplatelet formation, and altered TPO-dependent Ras/MAPK signaling. Similar effects on megakaryopoiesis are also observed in vitro following treatment with newly developed Shp2 inhibitors.

Strengths and Weaknesses:

The study addresses an important biological question and presents a substantial dataset that could contribute to a better understanding of Shp1 and Shp2 function in platelet biology. However, several aspects of data presentation and interpretation would benefit from additional clarification. In particular, while the authors conclude that single genetic deletion or pharmacological inhibition of Shp1 has a limited impact and that the major phenotypes are specific to combined Shp1/2 deletion or Shp2 inhibition, some of the data suggest more nuanced effects that may warrant further discussion.

We thank the reviewer for raising this point. The manuscript is being revised accordingly, including highlighting the potential role of Shp1 in megakaryopoiesis and thrombopoiesis under steady-state and stressed conditions, requiring more detailed investigation.

Reviewer #3 (Public review):

Summary:

In this manuscript, Barré et al utilize the Gp1ba-Cre transgenic mouse model to build upon previous findings in a Pf4-Cre system to investigate the effects of individual and combined Shp1 and Shp2 deletion in megakaryocytes and platelets. They report decreased megakaryocyte maturation, macrothrombocytopenia, and increased bleeding primarily in association with the Shp1/Shp2 double-knockout condition. The authors further show that this phenotype appears to be driven primarily by Shp2 and implicate dysregulation of Mpl signaling and downstream Ras/MAPK pathways, including ERK1/2. Given the key role of these pathways in human diseases such as myeloproliferative neoplasms and the challenges associated with modulating such a central pathway, identification of a specific regulator of Mpl signaling poses intriguing questions for future studies on clinical applicability.

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

Strengths:

Overall, the experiments combine in vitro, in vivo, and ex vivo approaches and appear to have been carefully designed and carried out, with multiple technical and biological replicates where relevant. The authors make a compelling argument for using the Gp1baCre as opposed to the Pf4-Cre system and demonstrate both the dose- and stagedependent effects of Shp1 and Shp2 on megakaryopoiesis and thrombopoiesis. They find that Shp1 and Shp2 are required in late-stage megakaryocyte maturation and that even low levels of expression compared to baseline are likely sufficient to yield generally normal megakaryocytes. Their findings also lead to specific future directions, such as the mechanism by which Shp1 regulates megakaryopoiesis and thrombopoiesis that is distinct from TPO-mediated signaling.

Weaknesses:

While the experiments have been thoughtfully designed and carried out, there is limited background explanation on relatively complex or niche pathways/mechanisms, such as the relationship between P-selectin, CRP, and PAR4p; the interactions between SFK, Syk, GPVI, and CLEC-2; and TPO, MPL, ERK1/2, AKT, and STAT3, which, while likely intuitive to experts in their respective fields, may be less obvious to a reader approaching this manuscript with a global interest in megakaryopoiesis/thrombopoiesis and thus detract from the impact of the findings.

We thank the reviewer for raising this point. The manuscript is being revised, to better explain the rationale and molecular mechanisms linking these pathways and functions.

With regard to the science itself, some of the conclusions feel premature based on the available data.

(1) The section "Aberrant ITAM signaling in Shp1- and Shp2-deficient platelets" is challenging to follow for those not well-versed in ITAM signaling and associated pathways, and may take additional outside reading to follow the conclusion that Syk-dependent signaling is modulated downstream of GPVI and CLEC-2 based on lack of change in Src p-Tyr418, especially considering that Src p-Tyr418 was previously introduced as a measure of SFK rather than Syk. In the introduction, Shp1 is specifically mentioned as a negative regulator of the ITAM/Syk/phospholipase pathway. However, in Figure 4Ai and Bi, Syk phosphorylation/activation in Shp1 knockout cells did not appear to be different from Shp2 knockout cells, and is lower than the control, which is surprising for a negative regulator. It is also not clear why, in the section (Figure 4A-B), there is reduced Syk activation in Shp1 and Shp2 single knockout cells upon CLEC2 stimulation (but apparently not with CRP) when there was no difference in response to CLEC2 (but a difference in response to CRP) in the previous section (Figure 3A, C).

We thank the reviewer for raising these important points. The manuscript is being revised accordingly, including clarifying the roles of SFKs, Shp1 and Shp2 in the ITAM-Syk-PLCg2 signaling pathway.

Briefly, SFKs are essential for phosphorylating ITAMs, allowing SH2-dependent docking of Syk. Reduced reactivity of Shp1/2 DKO platelets to CRP and collagen is likely due to downregulation of the ITAM-containing GPVI-FcR g-chain complex and integrin a2 subunit, and concomitant reduction in Syk phosphorylation.

However, the marginal albeit significant reduction in Syk phosphorylation downstream of CLEC-2 in Shp1 and Shp2 KO platelets was not determined and was insufficient to impact CLEC-2-mediated platelet aggregation under the conditions tested.

Differences in the stoichiometry and docking of Syk to phosphorylated GPVI-FcR g-chain and CLEC-2 likely contribute to the differences in platelet reactivity and Syk phosphorylation downstream of the two receptors in the absence of Shp1 and Shp2.

(2) In the section "Reduced Tpo signaling in Shp1/2-deficient MKs," only Western blot data for (p)ERK1/2, AKT, and STAT3 are presented before concluding that decreased ERK1/2 activity is a mechanistic explanation for thrombocytopenia seen in the Shp1/2 doubleknockout condition. Such a statement would benefit from additional experiments, such as protein or transcriptional levels of ERK1/2 targets specifically relevant to megakaryopoiesis, such as ETS, FOS, and JUN, to assess the consequences of decreased phosphorylated ERK1/2.

We thank the reviewers for these constructive comments. Further experiments are being planned to determine the biological and transcriptional consequences of reduced ERK1/2 phosphorylation during megakaryopoiesis and thrombopoiesis.

(3) Suggesting that "inhibiting Shp2 will not have any bleeding consequence in patients" and that Shp2 may be a therapeutic target in myeloproliferative neoplasms when none of these studies have been carried out in a human model is a bold conclusion. There are no data presented on, for example, whether Shp2 inhibition can help reverse the MPL/JAK/STAT pathway in the setting of gain-of-function mutations specifically associated with myeloproliferative neoplasms.

This conclusion is being tempered in the revised manuscript. Genetic- and pharmacological-based approaches will be used to establish the therapeutic potential of inhibiting Shp1 and Shp2 in mouse models of MPN, including Jak2 gain-of-function mice. Bleeding and thrombotic complications of inhibiting Shp1 and Shp2 will be explored as part of these studies.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer # 1 (Public review):

(1) Structure and Presentation of Results

• I recommend reordering the visual-cue experiments to progress from simpler conditions (no cues) to more complex ones (cue-conflict). This would improve narrative logic and accessibility for non-specialist readers. The authors have chosen not to implement this suggestion, which I respect, but my recommendation stands.

Thank you for this suggestion. We understand your point that presenting the experiments from simpler to more complex conditions may seem more intuitive. However, we have kept the original order because it better reflects the logic of the study itself. Our work first asked whether fall armyworms, like the Bogong moth, use a magnetic compass that is integrated with visual cues. Only after establishing this behavioral feature did we go on to test whether visual cues are required to maintain magnetic orientation. To make this reasoning clearer to readers, we have explicitly stated in the Introduction that magnetic orientation in the Bogong moth depends on the integration of visual cues, which provides clearer context for the experimental design.

(2) Ecological Interpretation

• The authors should expand their discussion on how the highly simplified, static cue setup translates to natural migratory conditions, where landmarks are dynamic, transient, or absent. Specifically, further consideration is needed on how the compass might function when landmarks shift position, become obscured, or are replaced by celestial cues. Additionally, the discussion would benefit from a more consolidated section with concrete suggestions for future experiments involving transient, multiple, or more naturalistic visual cues. This point was addressed partially in one paragraph of the Discussion, which reads as follows:

"In nature, they are likely to encounter a range of luminance-gradient visual cues, including relatively stable celestial cues as well as transient or shifting local features encountered en route. Although such natural cues differ from our simplified laboratory stimulus, they may represent intermittently sampled visual inputs that can be optimally integrated with magnetic information, with the congruency between visual and magnetic cues likely playing a key role in maintaining a stable compass response. Whether the cues are static or changing, brief periods without them may still allow the subsequent recovery of a stable long-distance orientation strategy. Determining which types of natural visual cues support the magnetic-visual compass, and how they interact with magnetic information, including how their momentary alignment or angular relationship is integrated and how such visual cue-magnetic field interactions may require time to influence orientation, together with elucidating the genetic and ecological bases of multimodal orientation, will be important objectives for future research." While this paragraph is informative, the wording remains lengthy, somewhat unclear, and vague. Shorter, clearer statements would improve readability and impact. For example:

• How could moths maintain direction during periods when only the magnetic field is present and visual landmarks are absent?

• Could celestial cues (e.g., stars) compensate, and what happens if these are also obscured?

• What role does saliency play when multiple visual landmarks are present simultaneously?

• How might a complex skyline without salient landmarks affect orientation?

Including simple, concise sentences that pose concrete open questions and suggest experimental designs would strengthen the discussion without creating space issues. In my view, a comprehensive discussion of how the simplified, static cue setup relates to natural migratory conditions-where landmarks are dynamic, transient, or absent-would add significant value to the paper.

Thank you for this constructive and insightful comment. You correctly point out that our articulation of the ecological relevance of the simplified, static cue setup was not sufficiently clear. We also agree that the original wording in the Discussion remained overly general. In the revised Discussion, we updated the manuscript to incorporate recently published findings on the use of light–dark gradients for orientation in fall armyworms. However, we explicitly note that it remains unclear whether fall armyworms can exploit naturally occurring luminance gradients, such as those generated by the moon, for orientation under natural conditions. We further emphasize that during natural migration the visual environment is dynamic, with celestial cues available intermittently and local visual features changing continuously during flight. In this context, we outline several key unresolved questions, including whether celestial cues can compensate when local landmarks are absent; how multiple visual cues are weighted and integrated with geomagnetic information; how transient visual cues (like moving clouds or changing illumination) influence orientation; and how luminance gradients that are common in natural nocturnal environments interact with the geomagnetic field to support orientation. For each of these issues, we briefly suggest experimental approaches to guide future research.

(3) Methodological Details and Reproducibility

• The lack of luminance level measurements should be explicitly highlighted.

Thank you for your helpful suggestion. You are right that luminance level is an important experimental parameter. We have stated this information in the Methods section under Behavioral apparatus: “The ambient light level in the experimental environment was measured to be below 1 lux using a Testo 540 lux meter (Testo SE & Co. KGaA, Titisee-Neustadt, Germany). Further work is still required to compare the illuminance used in this study with that under natural conditions, which are inherently variable.” This point is also clarified in the legend of Figure S3 in the supplementary material.

• The authors chose not to adjust figure legends by replacing "magnetic South" with "magnetic North." While I believe this would be more conventional and preferable, this is ultimately a minor stylistic issue.

Thank you very much for your suggestion. We understand your point and agree that using “magnetic North” would be more conventional. However, because our experiments focus on the orientation behavior of the autumn population, magnetic South is aligned with the landmark direction representing the potential migratory direction, which we believe makes the figures more intuitive for readers. We therefore consider this a minor stylistic issue.

(4) Conceptual Framing and Discussion

• Although the authors made a good attempt to explain the limitations of using an artificial visual cue, I believe there is room or a more explicit argument. For example, it could be stated clearly that this species is unlikely to encounter a situation in nature where a single, highly salient landmark coincides with its migratory direction. Therefore, how these findings translate to real migratory contexts remains an open question. A sentence or two making this point directly would strengthen the discussion.

Thank you for your helpful suggestion. We now address this point explicitly in the Discussion, noting that fall armyworms are unlikely to experience a natural visual environment dominated by a single, static, and highly salient landmark coinciding with their migratory direction. Consequently, how these findings translate to real migratory contexts remains an open question.

(5) Technical and Open-Science Points

• Sharing the R code openly (e.g., via GitHub) should be seriously considered. The code does not need to be perfectly formatted, but making it available would be highly beneficial from an open-science perspective.

Thank you for the suggestion. We agree that making code openly available is valuable from an open-science perspective. The MMRT script used in this study is Moore’s Modified Rayleigh Test, available from the original publication by Massy et al. (2021; https://doi.org/10.1098/rspb.2021.1805). In the previous version, we only cited this reference in the Materials and Methods section; we have now added a direct link to the script to improve clarity and accessibility. We have also provided a public link to the data-recording scripts used in the Flash Flight Simulator (https://doi.org/10.17632/6jkvpybswd.1). This repository additionally includes a map-based optical flow script that was not used in the present study but is shared for completeness.

Reviewer #1 (Recommendations for the authors):

• LL. 133-137 (end of paragraph starting with "The fall armyworm is a migratory crop pest native to the Americas"): Suggest splitting into shorter, clearer sentences. The limitations of this method could be better articulated here and elaborated in the Discussion.

Thank you for this suggestion. We have revised this paragraph by splitting it into shorter, clearer sentences and by articulating the limitations of this method more explicitly. These limitations are further elaborated in the Discussion.

• LL. 181-185 (end of paragraph starting with "To examine if fall armyworms integrate geomagnetic and visual cues for seasonal migratory orientation"): It would be helpful to state explicitly that season-specific headings have been confirmed in the lab using a flight simulator, but destination regions remain unknown without further tracking experiments.

Thank you for this helpful suggestion. We have now clarified in the revised manuscript that season-specific orientation headings have been confirmed in the laboratory using a flight simulator, while the actual migratory destination regions remain unclear in the absence of tracking experiments.

• LL. 230-234 (start of paragraph "Our previous research showed that fall armyworms reared under artificially simulated fall conditions…"): Clarify which migratory season is being referenced.

Thank you for this helpful suggestion. We have clarified in the text that the migratory season referenced here is the autumn migratory season. In addition, we have added information in the Methods to specify the actual calendar season during which the insects were reared under the simulated conditions.

• LL. 270-272 (middle of Fig. 2 caption): Suggest explicitly mentioning that for this population, the seasonally appropriate direction is southbound in autumn and northbound in spring, as this may not be clear to non-specialists.

Thank you for this helpful suggestion. We have now explicitly stated the seasonally appropriate migratory directions for this population, indicating southbound migration in autumn and northbound migration in spring, to improve clarity for non-specialist readers.

• LL. 421 (middle of paragraph starting with "We also considered the limitations of the Rayleigh test…"): Add that the groups lacking visual cues exhibited "lower directedness as per lower vector length (r)" in addition to lower flight stability.

Thank you for this helpful suggestion. We further note that the conclusions drawn from the flight stability analysis are consistent with those based on individual r-value analyses.

• LL. 499-501 ("unlike some vertebrates that can rely solely on magnetic information (Mouritsen, 2018)"): This point is slightly downplayed. It should be emphasized that nearly all tested vertebrates and invertebrates (e.g., birds, mole rats, fish, frogs, and other insects) demonstrate a magnetic compass without requiring visual landmarks. Moths are the only tested invertebrates so far that show landmark-magnetic field dependency for their magnetic compass to be manifested in a behavioural orientation response in Flight Simulator.

Thank you for this important comment. We agree that this point represents a key synthesis in the Discussion, as it concerns how our findings relate to, and differ from, magnetic orientation demonstrated in other animal groups. We have therefore expanded the Discussion to note that studies have shown that some animals can exhibit directional preferences in simplified visual environments solely in response to changes in the magnetic field, and we now cite representative examples from birds and mole rats. At the same time, we also acknowledge important methodological and phenotypic differences among taxa. In particular, moths’ magnetic orientation has been assessed using a flight simulator, a setup in which stable directional behavior must be actively maintained during continuous movement. This is an important difference from orientation assays in birds during take-off or in terrestrial mammals such as mole rats. Moreover, whether birds and other animals rely on visual input to detect or calibrate magnetic information under certain conditions remains an open question. We therefore emphasize here both the phenotypic differences observed across experimental systems and the methodological considerations.

• LL. 560-565 (paragraph starting with "Our flight simulator system (Dreyer et al., 2021) …"): Suggest clarifying what the Flash flight simulator system is and how it differs from the Mouritsen-Frost flight simulator.

Thank you for this suggestion. We have added a brief clarification of the Flash flight simulator and how it differs from the Mouritsen–Frost system.

• LL. 605-608 ("Spectral measurements …"): Explicitly mention that total illuminance was not measured and that further work is required to compare the illuminance used with natural conditions which of course vary.

Thank you for this helpful suggestion. We agree that total illuminance is an important factor. We have now added a statement noting that the ambient light level in the experimental environment was measured to be below 1 lux using a Testo 540 lux meter, and we further acknowledge that additional work is required to compare the illuminance used in this study with that under naturally variable conditions.

• LL. 628-641 (end of paragraph starting with "Electromagnetic noise at the experimental site ... "): Explain why this matters for interpreting behavioural responses. Highlight that although conditions were somewhat magnetically noisy which based on the past work may disrupt magnetic compass as it was shown in birds (eg Engels et al. 2014 Nature), the observed magnetic response under certain conditions indicates that the magnetic sense remained functional when landmark and magnetic field were aligned. This way you can pre-empt this criticism of your magnetic conditions being not ideal and noise on the left handside of the spectrum measured (which is not uncommon).

Thank you for this helpful suggestion. We have now cited Engels et al. (2014, Nature) in this section and expanded the text to explain why electromagnetic noise at the experimental site is relevant for interpreting the behavioural responses. We also clarify the rationale for measuring electromagnetic noise and discuss the observed low-frequency (“left-hand side”) noise in the spectrum.

• Fig. 51: Suggest adapting Y-axes and using violin or box plots (e.g., panels A/B starting from 30 up to 50, etc.).

Thank you for this helpful suggestion. We have revised Fig. 5 accordingly by adapting the Y-axis scaling and replacing the original plots with box plots, as suggested.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

The researchers aimed to identify which neurotransmitter pathways are required for animals to withstand chronic oxidative stress. This work thus has important implications for disease processes that are caused/linked to oxidative stress. This work identified specific neurotransmitters and receptors that coordinate stress resilience, both prior to and during stress exposure. Further, the authors identified specific transcriptional programs coordinated by neurotransmission that may provide stress resistance.

Strengths:

The manuscript is very clearly written with a well-formulated rationale. Standard C. elegans genetic analysis and rescue experiments were performed to identify key regulators of the chronic oxidative stress response. These findings were enhanced by transcriptional profiling that identified differentially expressed genes that likely affect survival when animals are exposed to stress.

We thank the reviewer for their positive assessment.

Weaknesses:

Where the gar-3 promoter drives expression was not discussed in the context of the rescue experiments in Figure 7.

We now provide information about expression using 7.5 kb gar-3 promoter fragment  and compare directly with our analysis of endogenous gar-3 expression using the genome-modified gar-3::SL2::GFP strain (Page 16, new Figures 8 and S3).

Reviewer #1 (Recommendations for the authors):

(1) Figure 3B is not mentioned in the text.

Fixed. Figure 3B is now called out on page 10 of the revised manuscript.

(2) The rationale for using the specific PQ concentration was not provided.

We selected this concentration based on its use for chronic assays by other studies in the field to allow for direct comparison with our results. We now clarify this point in the Methods section (Page 26 of the revised text).

(3) Transgenic animals injected with the unc-17βp::gar-3 transgene (25 ng/μL) displayed strikingly increased survival in the presence of 4 mM PQ compared to either gar-3 mutants or wild type (should have a Figure cited here)

Fixed. Figure 9E is now referenced on Page 19 of the revised text.

(4) The text describing Figure 7C details a comparison with the gar-3 single mutant but the graph shows the unc-17 single mutant

Figure 7C is a comparison of the survival of gar-3 single mutants with either wild type or gar-3;ric-3 double mutants as described in the text.

Reviewer #2 (public comments)

In this paper, Biswas et al. describe the role of acetylcholine (ACh) signaling in protection against chronic oxidative stress in C. elegans. They showed that disruption of ACh signaling in either unc-17 mutants or gar-3 mutants led to sensitivity to toxicity caused by chronic paraquat (PQ) treatment. Using RNA seq, they found that approximately 70% of the genes induced by chronic PQ exposure in wild type failed to upregulate in these mutants. The overexpression of gar-3 selectively in cholinergic neurons was sufficient to promote protection against chronic PQ exposure in an ACh-dependent manner. The study points to a previously undescribed role for ACh signaling in providing organism-wide protection from chronic oxidative stress, likely through the transcriptional regulation of numerous oxidative stressresponse genes. The paper is well-written, and the data are robust, though some conclusions seem preliminary and do not fully support the current data. While the study identifies the muscarinic ACh receptor gar-3 as an important regulator of the response to PQ, the specific neurons in which gar-3 functions were not unambiguously identified, and the sources of ACh that regulate GAR-3 signaling and the identities of the tissues targeted by gar-3 were not addressed, limiting the scope of the study.

We thank the reviewer for their positive assessment. We provide additional data and discussion of the points raised by the reviewer in the revised manuscript. In particular, as suggested by the reviewer, we conducted additional tissue-specific rescue experiments to try to better define GAR-3 site of action. We found that specific rescue of gar-3 expression in either cholinergic motor neurons or muscles each provide partial rescue. In addition, we quantified the expression of the nhr-185 and fbxa-73 genes, identified as upregulated by PQ in our RNA-seq studies, following oxidative stress (new Fig. S4). We observed increased expression of both genes following PQ exposure, providing independent confirmation for transcriptional upregulation of these genes as part of the stress response. See the responses to points #1 and #3 below for additional details.

Major Comments:

(1) The site of action of cholinergic signaling for protection from PQ was not adequately explored. The authors' conclusion that cholinergic motor neurons are protective is based on studies using overexpression of gar-3 and an unc-17 allele that may selectively disrupt ACh in cholinergic motor neurons (Figure 9F), but these approaches are indirect. To more directly address the site of action, the authors should conduct rescue experiments using well-defined heterologous promoters. Figure 7G shows that gar-3 expressed under a 7.5 kb promoter fragment fully rescues the defect of gar-3 mutants, but the authors did not report where this promoter fragment is expressed, nor did they conduct rescue experiments of the specific tissues where gar-3 is known to be expressed (cholinergic neurons, GABAergic neurons, pharynx, or muscles). UNC-17 rescue experiments could also be useful to address the site of action. Does expression of unc-17 selectively in cholinergic motor neurons rescue the stress sensitivity of unc-17 mutants (or restore resistance to gar-3(OE); unc-17 mutants)? These experiments may also address whether ACh acts in an autocrine or paracrine manner to activate gar-3, which would be an important mechanistic insight to this study that is currently lacking.

We performed additional rescue experiments using heterologous promoters to drive gar-3 expression in cholinergic neurons or muscle and found that each provided a small, but significant degree of rescue as assessed from Kaplan-Meier survival curves. These results are presented in Figure 8 of the revised manuscript. We have not conducted similar unc-17 rescue experiments; however, we point out that cellspecific unc-17 knockdown by RNAi using the unc-17b promoter (expression largely restricted to ventral cord ACh motor neurons) increases sensitivity to PQ in our long-term survival assays (Figure 3A). Combined with our analysis of unc-17(e113) mutants, we believe these results support a requirement for unc-17 expression in cholinergic motor neurons.

(2) The genetic pan-neuronal silencing experiments presented in Figure 1 motivated the subsequent experiments, but the authors did not relate these observations to ACh/gar-3 signaling. For example, the authors did not address whether silencing just the cholinergic motor neurons at the different times tested has the same effects on survival as pan-neuronal silencing.

We used the pan-neuronal silencing to motivate further analysis of various neurotransmitter systems. Our genetic studies implicate both glutamatergic and cholinergic systems in protective responses to oxidative stress. The effects of pan-neuronal silencing on survival during long-term PQ exposure may therefore be derived solely from cholinergic neurons, glutamatergic neurons, or a combination of both neuronal populations. Distinguishing between these possibilities may be quite complicated and is not central to the main message of our paper. We therefore suggest this additional analysis lies outside the scope of this revision. Nonetheless, to address the reviewer’s point, in the revised text we expand our discussion relating the pan-neuronal silencing results to our analysis of ACh signaling (pages 21-22).

(3) It is assumed that protection occurs through inter-tissue signaling of ACh to target tissues, where it impacts gene expression. While this is a reasonable assumption, it has not been directly shown here. It is recommended that the authors examine GFP reporter expression of a sampling of the genes identified in this study (including proteasomal genes that the authors highlight) that are regulated by unc-17 and gar-3. This would serve to independently confirm the RNAseq data and to identify target tissues that are subject to gene expression regulation by ACh, which would significantly strengthen the study.

Agreed. To address this question, we investigated expression of the nhr-185 and fbxa-73 genes implicated as upregulated by oxidative stress in our RNA-seq studies. Consistent with our RNA-seq findings, we observed significantly increased expression of a nhr-185pr::GFP transcriptional reporter, primarily in the pharynx and anterior intestine, following 48 hrs of PQ exposure. These results support transcriptional upregulation of expression in these tissues as part of the stress response. fbxa-73 was among the proteasomal genes implicated as oxidative stress-responsive by RNA-seq. Consistent with this finding, by quantitative RT-PCR we observed a significant increase in fbxa-73 expression in wild type animals following 48 hrs of PQ treatment. These new results provide independent confirmation of the gene expression changes we observed by RNA-seq and are now included in new Figure S4 and discussed on Pages 17-18 of the revised manuscript.

Reviewer #2 (Recommendations for the authors):

(1) As an independent way of addressing whether enhanced ACh signaling is sufficient for protection, the authors could examine stress resistance in ace mutants, as was reported in PMID: 39097618, or in mutants with increased ACh secretion.

We thank the reviewer for this suggestion. We are pursuing the impacts of increased cholinergic activation in a separate study. We are pursuing experiments along the lines the reviewer suggests as one facet of this independent study. Our findings here provide evidence that increasing GAR-3 signaling in ACh motor neurons by cell-specific overexpression enhances protection. 

(2) To address the specificity of ACh signaling by gar-3 for this response, the authors could report survival data for mutants lacking each of the other two mACh receptors, gar-1 and gar-2.

We thank the reviewer for this suggestion. We now include new data showing that gar-3;gar-2 double mutants have similar survival to gar-3 single mutants in the presence of PQ new Figure 7F). We agree that further studies of additional GPCRs (e.g. gar-1 and metabotropic glutamate receptors) will be required to definitively establish specificity for GAR-3 and we now acknowledge this point on page 15 of the revised text.

(3) Do carbonylation levels correlate with toxicity? For example, do gar-3 mutants have more carbonylation and gar-3 OE have less?

This is an interesting question. To try to address this, we performed additional protein carbonylation experiments for unc-17 and gar-3 mutants. We found a similar increase in protein carbonylation following PQ exposure for gar-3 mutants as observed for wild type; however, we also noted a higher level a batch-to-batch variability for gar-3 compared with wild type and are therefore hesitant to draw firm conclusions. We have not included these data in the revised manuscript but provide them for the reviewer’s information here (Author response image 1 shows our prior N2 data for comparison). We were not able to conduct similar experiments for unc-17 mutants because we noted local starvation when the animals were grown at the high density required to obtain the protein quantities needed for these experiments.

Author response image 1.

(4) Citations in text for Figures 4A and 8A are missing.

Fixed. Figures 4A and 8A (now 9A) are cited on pages 10 and 17 of the revised text, respectively.

(5) Figures 4-6 and 8 have limited information content. Condense or move to supplementary.

While we acknowledge the reviewer’s viewpoint here, we believe that the analyses of the transcriptional responses described in Figures 4-6 and 8 are central to the study. To address reviewers’ comments, we have included a new Figure 8 and merged previous Figures 8 and 9 (new Figure 9) in the revised manuscript.

(6) "expression of" is repeated in "Finally, transgenic expression of expression of a wild-type GAR-3::YFP"

Fixed.

Author response:

The following is the authors’ response to the original reviews

eLife Assessment

This important study shows that orientation tuning of V1 neurons is suppressed during a continuous flash suppression paradigm, especially when the neurons have a binocular receptive field. However, the evidence presented is incomplete and, in particular, does not distinguish whether this suppression is due to reduced contrast or due to masking.

This assessment is primarily based on the critique of Reviewer 2 that our results do not distinguish whether the impact of CFS is due to reduced contrast or due to masking. Reviewer 2 referred to Yuval-Greenberg and Heeger (2013), noting that: “V1 activity is, in fact, reduced during CFS … the mask reduces the gain of neural responses to the grating stimulus … making it invisible in the same way that reducing contrast makes a stimulus invisible.” To be precise, Yuval-Greenberg and Heeger (2013) used “akin to”, instead of “the same way”, in their abstract.

We agree that CFS masking and contrast reduction can both lower the signal-to-noise ratio and thereby reducing visibility. However, these two factors operate in fundamentally different ways. According to gain control models by Heeger and others, reducing the physical contrast of a stimulus decreases the excitatory drive, while dichoptic masking increases the normalization pool. Our findings therefore reflect genuine masking-induced suppression and are not attributable to stimulus contrast reduction.

Public Reviews:

Reviewer #1 (Public review):

Disclaimer: While I am familiar with the CFS method and the CFS literature, I am not familiar with primate research or two-photon calcium imaging. Additionally, I may be biased regarding unconscious processing under CFS, as I have extensively investigated this area but have found no compelling evidence in favor of unconscious processing under CFS.

This manuscript reports the results of a nonhuman-primate study (N=2 behaving macaque monkeys) investigating V1 responses under continuous flash suppression (CFS). The results show that CFS substantially suppressed V1 orientation responses, albeit slightly differently in the two monkeys. The authors conclude that CFS-suppressed orientation information "may not suffice for high-level visual and cognitive processing" (abstract).

The manuscript is clearly written and well-organized. The conclusions are supported by the data and analyses presented (but see disclaimer). However, I believe that the manuscript would benefit from a more detailed discussion of the different results observed for monkeys A and B (i.e., inter-individual differences), and how exactly the observed results are related to findings of higher-order cognitive processing under CFS, on the one hand, and the "dorsal-ventral CFS hypothesis", on the other hand.

Thanks for reviewer’s helpful comments and suggestions. We added new contents discussing the inter-individual differences and the "dorsal-ventral CFS hypothesis" in the revision, and made other changes, which are detailed below.

Major Comments:

(1) Some references are imprecise. For example, l.53: "Nevertheless, two fMRI studies reported that V1 activity is either unaffected or only weakly affected (Watanabe et al., 2011; Yuval-Greenberg & Heeger, 2013)". "To the best of my understanding, the second study reaches a conclusion that is entirely opposite to that of the first, specifically that for low-contrast, invisible stimuli, stimulus-evoked fMRI BOLD activity in the early visual cortex (V1-V3) is statistically indistinguishable from activity observed during stimulus-absent (mask-only) trials. Therefore, high-level unconscious processing under CFS should not be possible if Yuval-Greenberg & Heeger are correct. The two studies contradict each other; they do not imply the same thing.

Sorry we did not make our point clear. Our original concern was that the effects of CFS on V1 activity were underestimated, even in Yuval-Greenberg & Heeger (2013), as both studies compared monocular and dichoptic masking to estimate the influence of visibility. In contrast, in original psychophysical studies, the CFS effect was compared with or with dichoptic masking, which is expected to be stronger. We rewrote the paragraph to clarify.

“Two prominent fMRI studies have examined the impact of CFS on V1 activity (Watanabe et al., 2011; Yuval-Greenberg & Heeger, 2013). Watanabe et al. (2011) compared monocular CFS masking (stimulus visible) and dichoptic CFS masking (stimulus invisible), and reported that V1 BOLD responses were largely insensitive to stimulus visibility when attention was carefully controlled. However, using similar experimental design, Yuval-Greenberg and Heeger (2013) observed reduced BOLD responses in V1 under dichoptic masking, suggesting that V1 activity changed with stimulus visibility. They attributed the difference of results between two studies mainly to differences in statistical power (~250 trials per condition vs. ~90 trials per condition). Nevertheless, these studies were not designed to quantify the pure effect of CFS on stimulus-evoked V1 responses, as they contrasted monocular and dichoptic masking conditions to equate stimulus input while manipulating perceptual visibility. In contrast, original psychophysical studies (Tsuchiya & Koch, 2005; Tsuchiya, Koch, Gilroy, & Blake, 2006) demonstrated CFS masking by contrasting the visibility of the target stimulus with and without the presence of dichoptic mask. It is apparent that the pure CFS impact in above fMRI studies would be the difference of BOLD signals between binocular masking and stimulus alone conditions. In other words, the impact of CFS on V1 activity should be larger than what has been reported by Yuval-Greenberg and Heeger (2013).” (lines 55-71)

(2) Line 354: "The flashing masker was a circular white noise pattern with a diameter of 1.89°, a contrast of 0.5, and a flickering rate of 10 Hz. The white noise consisted of randomly generated black and white blocks (0.07 × 0.07 each)." Why did the authors choose a white noise stimulus as the CFS mask? It has previously been shown that the depth of suppression engendered by CFS depends jointly on the spatiotemporal composition of the CFS and the stimulus it is competing with (Yang & Blake, 2012). For example, Hesselmann et al. (2016) compared Mondrian versus random dot masks using the probe detection technique (see Supplementary Figure S4 in the reference below) and found only a poor masking performance of the random dot masks.

Yang, E., & Blake, R. (2012). Deconstructing continuous flash suppression. Journal of Vision, 12(3), 8. https://doi.org/10.1167/12.3.8

Hesselmann, G., Darcy, N., Ludwig, K., & Sterzer, P. (2016). Priming in a shape task but not in a category task under continuous flash suppression. Journal of Vision, 16, 1-17.

In a previous human psychophysical study, we also used the same noise pattern and the CFS effect appeared to be robust (Xiong et al., 2016, https://doi.org/10.7554/eLife.14614). However, we believe that the reviewer made a good point, and weaker suppression due to the use of our stimulus pattern may have contributed to the weaker suppression in Monkey B. This issue is now discussed in the revision regarding the individual variability in our results.

“In addition, the random-noise masker we used might not be as effective as Mondrian patterns (G. Hesselmann, Darcy, Ludwig, & Sterzer, 2016). If reduced stimulus contrast and a Mondrian masker were used, we predict that CFS suppression in Monkey B would strengthen, potentially approaching the level observed in Monkey A. Nevertheless, it is worth emphasizing that our main conclusions are primarily based on data from Monkey A, who exhibited much stronger CFS suppression.” (lines 321-327)

(3) Related to my previous point: I guess we do not know whether the monkeys saw the CF-suppressed grating stimuli or not? Therefore, could it be that the differences between monkey A and B are due to a different individual visibility of the suppressed stimuli? Interocular suppression has been shown to be extremely variable between participants (see reference below). This inter-individual variability may, in fact, be one of the reasons why the CFS literature is so heterogeneous in terms of unconscious cognitive processing: due to the variability in interocular suppression, a significant amount of data is often excluded prior to analysis, leading to statistical inconsistencies.

Yamashiro, H., Yamamoto, H., Mano, H., Umeda, M., Higuchi, T., & Saiki, J. (2014). Activity in early visual areas predicts interindividual differences in binocular rivalry dynamics. Journal of Neurophysiology, 111(6), 1190-1202. https://doi.org/10.1152/jn.00509.2013

The individual difference issue is now explicitly addressed in the Discussion:

“Interocular suppression under CFS is known to vary substantially across individuals (Blake, Goodman, Tomarken, & Kim, 2019; Gayet & Stein, 2017; Yamashiro et al., 2013). This inter-individual variability may contribute to the heterogeneity observed in the CFS literature. We also found that the strength of V1 response suppression during CFS differed between two monkeys, as reflected by population orientation tuning functions (Fig. 2C), Fisher information (Fig. 2F), and reconstruction performance by the transformer (Fig. 3E). Several experimental factors may have contributed to the relatively weaker suppression observed in Monkey B. Because monkeys viewed the stimuli passively, we could not determine the dominant eye for each monkey (instead we switched the eyes and averaged the results), and the target was presented at relatively high contrast. Both factors are known to reduce the effectiveness of CFS suppression (Yang, Blake, & McDonald, 2010; Yuval-Greenberg & Heeger, 2013). In addition, the random-noise masker we used might not be as effective as Mondrian patterns (G. Hesselmann, Darcy, Ludwig, & Sterzer, 2016). If reduced stimulus contrast and a Mondrian masker were used, we predict that CFS suppression in Monkey B would strengthen, potentially approaching the level observed in Monkey A. Nevertheless, it is worth emphasizing that our main conclusions are primarily based on data from Monkey A, who exhibited much stronger CFS suppression.” (lines 311-327)

Moreover, the authors' main conclusion (lines 305-307) builds on the assumption that the stimuli were rendered invisible, but isn't this speculation without a measure of awareness?

We agree. To correct, we have removed the original lines 305-307 discussing the consciousness perception and reframed the manuscript throughout to focus on the impact of CFS on neural coding rather than on perceptual awareness. For example, the title has been changed to:

“Continuous flashing suppression of neural responses and population orientation coding in macaque V1”,

and the ending line of Introduction was changed to:

“This approach enabled us to investigate the potentially differential impacts of CFS on the responses of V1 neurons with varying ocular preferences, as well as apply machine learning tools to understand the impacts of CFS on V1 stimulus coding at the population level.” (lines 81-83)

(4) The authors refer to the "tool priming" CFS studies by Almeida et al. (l.33, l.280, and elsewhere) and Sakuraba et al. (l.284). A thorough critique of this line of research can be found here:

Hesselmann, G., Darcy, N., Rothkirch, M., & Sterzer, P. (2018). Investigating Masked Priming Along the "Vision-for-Perception" and "Vision-for-Action" Dimensions of Unconscious Processing. Journal of Experimental Psychology. General. https://doi.org/10.1037/xge0000420

This line of research ("dorsal-ventral CFS hypothesis") has inspired a significant body of behavioral and fMRI/EEG studies (see reference for a review below). The manuscript would benefit from a brief paragraph in the discussion section that addresses how the observed results contribute to this area of research.

Ludwig, K., & Hesselmann, G. (2015). Weighing the evidence for a dorsal processing bias under continuous flash suppression. Consciousness and Cognition, 35, 251-259. https://doi.org/10.1016/j.concog.2014.12.010

In the revision, we added a new paragraph to discussion issues related to the dorsal-ventral CFS hypothesis.

“A related issue is the dorsal-ventral CFS hypothesis, which proposes that CFS suppression may disproportionately affect ventral visual processing while relatively preserving dorsal pathways involved in visuomotor functions, potentially allowing category- or action-related information to remain accessible under suppression (Fang & He, 2005). However, subsequent fMRI studies have failed to provide consistent support for this dissociation, reporting either stream-invariant awareness effects (Guido Hesselmann & Malach, 2011; Ludwig et al., 2015; Tettamanti et al., 2017), residual signal in ventral rather than dorsal regions (Fogelson et al., 2014; Guido Hesselmann et al., 2011), or residual low-level feature information/partial visibility rather than preserved dorsal processing (Ludwig et al., 2015). Although our study does not directly test dorsal-ventral dissociations, our V1 results provide a constraint on what information downstream visual pathways could access under suppression. When CFS- induced interocular suppression was strong enough and stimuli reconstruction was markedly reduced, as in the case of Monkey A, the information required for category-level or action-related processing may not be sufficient for high-level cortical representation.” (lines 297-310)

Reviewer #2 (Public review):

Summary:

The goal of this study was to investigate the degree to which low-level stimulus features (i.e., grating orientation) are processed in V1 when stimuli are not consciously perceived under conditions of continuous flash suppression (CFS). The authors measured the activity of a population of V1 neurons at single neuron resolution in awake fixating monkeys while they viewed dichoptic stimuli that consisted of an oriented grating presented to one eye and a noise stimulus to the other eye. Under such conditions, the mask stimulus can prevent conscious perception of the grating stimulus. By measuring the activity of neurons (with Ca2+ imaging) that preferred one or the other eye, the authors tested the degree of orientation processing that occurs during CFS.

Strengths:

The greatest strength of this study is the spatial resolution of the measurement and the ability to quantify stimulus representations during CSF in populations of neurons, preferring the eye stimulated by either the grating or the mask. There have been a number of prominent fMRI studies of CFS, but all of them have had the limitation of pooling responses across neurons preferring either eye, effectively measuring the summed response across ocular dominance columns. The ability to isolate separate populations offers an exciting opportunity to study the precise neural mechanisms that give rise to CFS, and potentially provide insights into nonconscious stimulus processing.

Weaknesses:

While this is an impressive experimental setup, the major weakness of this study is that the experiments don't advance any theoretical account of why CFS occurs or what CFS implies for conscious visual perception. There are two broad camps of thinking with regard to CFS. On the one hand, Watanabe et al. (2011) reported that V1 activity remained intact during CFS, implying that CFS interrupts stimulus processing downstream of V1. On the other hand, Yuval-Greenberg and Heeger (2013) showed that V1 activity is, in fact, reduced during CFS. By using a parametric experimental design, they measured the impact of the mask on the stimulus response as a function of contrast and concluded that the mask reduces the gain of neural responses to the grating stimulus. They presented a theoretical model in which the mask effectively reduced the SNR of the grating, making it invisible in the same way that reducing contrast makes a stimulus invisible.

We used multi-class SVM (as suggested by reviewer 3) and a transformer-based model to examine the impact of CFS on the classification of 12 orientations spaced in 15o gaps, which resembles coarse orientation discrimination, as well as on stimulus reconstruction, which resembles stimulus perception necessary for high-level cognitive tasks, respectively. The results suggest that under CFS, an observer may still be able to perform coarse orientation discrimination but not high-level cognitive tasks. These findings provide new insights into the implications of CFS for conscious visual perception from a population decoding perspective.

In the revision, we also added a new paragraph discussing the implications of our findings for the dorsal-ventral CFS hypothesis, as suggested by reviewer 1. We previously presented a gain control model for our neuronal data in a VSS talk. However, we later decided that, since there are already nice models by Heeger and others, it would be better present something more unique and novel (i.e., machine learning results), which has now become a major component of the manuscript. We welcome the reviewer’s comments on this part.

An important discussion point of Yuval-Greenberg and Heeger is that null results (such as those presented by Watanabe et al.) are difficult to interpret, as the lack of an effect may be simply due to insufficient data. I am afraid that this critique also applies to the present study.

We are very much puzzled by the reviewer’s critique. First, our main result is not a null effect. A null effect would mean that CFS masking had no impact on population orientation responses. Instead, we observed a significant suppression or abolished tuning, which clearly indicates a strong effect of dichoptic masking. Second, our findings are based on large neural populations recorded using two-photon imaging, providing extensive sampling and statistical power. Thus, we believe that the reviewer’s critique about “insufficient data” are not applicable to our study.

Here, the authors report that CFS effectively 'abolishes' tuning for stimuli in neurons preferring the eye with the grating stimulus. The authors would have been in a much stronger position to make this claim if they had varied the contrast of the stimulus to show that the loss of tuning was not simply due to masking.

We are sorry that we cannot follow the logic here either. Even if “the mask effectively reduced the SNR of the grating, making it invisible in the same way that (“akin to”, to be more precise according to the abstract of Yuval-Greenberg and Heeger (2013)) reducing contrast makes a stimulus invisible”, it does not necessarily mean that dichoptic masking and contrast reduction are the same process or are based on the same neuronal mechanisms. According to gain control models by Heeger and others, reducing the stimulus contrast decreases the excitatory drive, while dichoptic masking increases the normalization pool via interocular suppression, both of which lower SNR, but are two fundamentally distinct processes.

Therefore, varying the stimulus contrast might reveal a main effect of contrast, and possibly an interaction between contrast and dichoptic masking, but it would neither prove nor disprove the main effect of dichoptic masking.

So, while this is an incredibly impressive set of measurements that in many ways raises the bar for in vivo Ca2+ imaging in behaving macaques, there isn't anything in the results that constitutes a real theoretical advance.

We sincerely hope that the reviewer would have a better judgment after reading our responses.

Reviewer #3 (Public review):

Summary:

In this study, Tang, Yu & colleagues investigate the impact of continuous flash suppression (CFS) on the responses of V1 neurons using 2-photon calcium imaging. The report that CFS substantially suppressed V1 orientation responses. This suppression happens in a graded fashion depending on the binocular preference of the neuron: neurons preferring the eye that was presented with the marker stimuli were most suppressed, while the neurons preferring the eye to which the grating stimuli were presented were least suppressed. The binocular neuron exhibited an intermediate level of suppression.

Strengths:

The imaging techniques are cutting-edge, and the imaging results are convincing and consistent across animals.

Weaknesses:

I am not totally convinced by the conclusions that the authors draw based on their machine learning models.

Thanks for pointing this issue. We have used a new multi-class SVM suggested by the reviewer to reanalyze the data and found similar results, which is detailed later.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Lines 56-63: "As a result, the dichoptic CFS masking, which is cortical, could be substantially stronger than monocular masking when accounting for the pre-cortical effects of monocular masking." I don't quite understand this argument. Could you please elaborate?

We have revised our writing to address the reviewer’s first major comment, which the current issue is related. The elaboration is highlighted in the paragraph below.

“Two prominent fMRI studies have examined the impact of CFS on V1 activity (Watanabe et al., 2011; Yuval-Greenberg & Heeger, 2013). Watanabe et al. (2011) compared monocular CFS masking (stimulus visible) and dichoptic CFS masking (stimulus invisible), and reported that V1 BOLD responses were largely insensitive to stimulus visibility when attention was carefully controlled. However, using similar experimental design, Yuval-Greenberg and Heeger (2013) observed reduced BOLD responses in V1 under dichoptic masking, suggesting that V1 activity changed with stimulus visibility. They attributed the difference of results between two studies mainly to differences in statistical power (~250 trials per condition vs. ~90 trials per condition). Nevertheless, these studies were not designed to quantify the pure effect of CFS on stimulus-evoked V1 responses, as they contrasted monocular and dichoptic masking conditions to equate stimulus input while manipulating perceptual visibility. In contrast, original psychophysical studies (Tsuchiya & Koch, 2005; Tsuchiya, Koch, Gilroy, & Blake, 2006) demonstrated CFS masking by contrasting the visibility of the target stimulus with and without the presence of dichoptic mask. It is apparent that the pure CFS impact in above fMRI studies would be the difference of BOLD signals between binocular masking and stimulus alone conditions. In other words, the impact of CFS on V1 activity should be larger than what has been reported by Yuval-Greenberg and Heeger (2013).” (lines 55-71)

(2) Line 13 low-level stimulus (properties).

Fixed, thanks.

Reviewer #3 (Recommendations for the authors):

Major comments:

(1) My main comment is regarding the SVM classifiers. The pair-wise (adjacent orientation pairs) decoding approach is unrealistic in my opinion and likely explains the very high accuracies that are reported. I believe that a multi-way classification approach - Linear Discriminant Analysis, Decision Trees, etc. - is needed to draw reasonable conclusions. Even SVMs can be adapted for multi-way classification (e.g., Allwein et al., 2000, J. Machine Learning Research).

Following the reviewer’s advice, we reanalyzed the data using a multi-class SVM with a one-vs-one (OvO) scheme to classify 12 orientations (Allwein et al., 2000), which yielded similar results.

“For orientation classification, we trained an all-pair multiclass support vector machine (SVM) classifier to discriminate 12 orientations based on trial-by-trial population neural responses from all trials (Allwein, Schapire, & Singer, 2000). Decoders for different FOVs, ipsilateral/contralateral target presentations, and baseline vs. CFS conditions were trained separately. Under the baseline condition, the decoders achieved mean classification accuracies of 89.5 ± 2.0% and 91.5 ± 2.1% across ipsilateral and contralateral eye conditions in Monkeys A and B, respectively, in contrast to a chance level of 8.3% (1 out of 12). Under CFS, decoding accuracy slightly decreased in Monkey A (81.7 ± 1.9%) but remained stable in Monkey B (90.4 ± 2.1%, Fig. 3A). These results suggest that under CFS, there is still sufficient information for coarse orientation discrimination, even for Monkey A whose V1 neuronal responses were substantially suppressed.” (lines 171-181)

(2) The inconsistent modeling results (Figure 3E,F) are puzzling and need to be adequately addressed.

SSIM and orientation error in original Fig. 3E, F measured the same reconstruction quality, but these two indices go in opposite directions for the same modeling results. To avoid confusion, we have removed the orientation error metric and now only report SSIM.

“We used a structural similarity index (SSIM) (Brunet, Vrscay, & Wang, 2012) to quantify the reconstruction performances. Across the grating-presenting ipsilateral and contralateral eyes, the baseline models reconstructed the grating with median SSIMs of 0.52 and 0.61 for the two FOVs of Monkey A, and 0.57 and 0.63 for the two FOVs of Monkey B, respectively, while the corresponding SSIMs for the CFS models were 0.16 and 0.19 for Monkey A, and 0.55 and 0.53 for Monkey B (Fig. 3E).” (lines 200-206)

Minor points:

(1) The phrase "perceptual consequences" in the title is somewhat strong and possibly misleading, since there are no behavioral measures in this study.

To address this concern from this reviewer and reviewer 1, we now focus on the impact of CSF on population orientation coding rather than perceptual consequences, which is more appropriate describing our modeling results. For example, we changed the title to: “Continuous flashing suppression of neural responses and population orientation coding in macaque V1“. Other changes are also made throughout the manuscript accordingly.

(2) Figure 4: Panel "F" is not marked in the figure.

Fixed, thanks.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

This study by Li and colleagues examines how defensive responses to visual threats during foraging are modulated by both reward level and social hierarchy. Using a naturalistic paradigm, the authors test how the availability of water or sucrose, with sucrose being more rewarding than water, shapes escape behavior in mice exposed to looming stimuli of different intensities, which are used to probe perceived threat level and defensive responses. In parallel, the study compares dominant and subordinate animals to assess how social rank biases the trade off between reward seeking and threat avoidance. By combining detailed behavioral analyses with computational modeling, the work addresses how reward level and social context jointly influence escape decisions in an ethologically relevant setting.

Across the different experimental conditions, perceived threat level is the main determinant of behavior. The authors show that looming stimuli associated with higher threat (contrast) consistently elicit faster and more robust escape responses than lower threat stimuli. This effect is particularly evident during early exposures, when animals are highly vigilant and have not yet habituated to the looming stimulus (learned that it is not dangerous). Later they described that as animals gain experience and habituate, behavior becomes more flexible, and reward level begins to exert a graded modulation of the escape response. Importantly, the authors show that under high threat conditions increasing reward value leads to more frequent and faster escape rather than greater reward pursuit. This finding is particularly relevant, as it suggests that highly valued rewards can heighten vigilance and thereby enhance responsiveness to threat, highlighting that reward does not simply compete with defensive behavior but can also reshape it depending on the perceived level of danger, in contrast to low threat conditions, where threat can be more easily outweighed by reward. Thus, an important conceptual contribution of the study is the introduction of vigilance as a useful framework to interpret these effects. Vigilance is treated as a behavioral state reflecting heightened attention to potential danger. In line with what is known from natural foraging, mice initially maintain high vigilance when confronted with an innate threat. This perspective helps clarify a finding that might otherwise appear counterintuitive. One might expect higher rewards to motivate animals to tolerate risk, explore more, and habituate faster in any scenario. Instead, the data suggest that highly rewarding outcomes can elevate vigilance, making animals more responsive to threat and leading to faster or more frequent escape under high threat conditions. In this sense, reward does not simply compete with threat but can also amplify sensitivity to it, depending on the internal state of the animal.

The social results are particularly interesting in this context as well. Dominant mice consistently prioritize avoidance over reward, showing stronger escape responses and slower habituation than subordinates. This behavior is well captured by the vigilance framework proposed by the authors: dominant animals appear to maintain higher vigilance, which biases decisions toward threat avoidance. The authors further suggest that stable social relationships sustain high vigilance and slow habituation, framing this as an evolutionarily conserved strategy that may enhance survival. This interpretation provides a valuable perspective on how social structure shapes defensive behavior beyond immediate physical interactions. At the same time, there are important limitations to this interpretation. All experiments were conducted in male mice, and it is possible that the relationship between social hierarchy, vigilance, and defensive behavior would differ substantially in females. In addition, the idea that stable social relationships maintain elevated vigilance does not straightforwardly align with broader views of social stability as protective for mental health and as a buffer against anxiety and stress. These points do not undermine the findings but suggest that the social effects described here should be interpreted with caution and within the specific context of the task and sex studied.

We thank the reviewer for raising this important point. In the context of repeated looming exposure, slower habituation reflects more sustained vigilance over time. Compared to individually housed mice, group-housed mice exhibit slower habituation (Lenz et al., 2022), and pair-housed mice showed even slower habituation in our current work. Importantly, this pattern does not indicate that pair-housed mice have higher overall vigilance than individually housed animals. Although individually housed mice habituate more quickly, they display higher initial vigilance, as reflected by their increased probability of escaping in response to looming stimuli (Lenz et al., 2022). Thus, pair-housed mice exhibited reduced defensive responses compared to individually housed animals, consistent with a social buffering effect.

Furthermore, in a separate study (Rank- and Threat-Dependent Social Modulation of Innate Defensive Behaviors; Li, Gao, Li, 2026, eLife 15:RP109571), we directly compared responses to looming stimuli when mice were tested alone versus in the presence of a social partner and observed clear evidence of social buffering.

Another important limitation is that the neural mechanisms underlying these effects remain speculative. The manuscript includes an extensive discussion of candidate circuits, particularly involving the superior colliculus and downstream structures, but this section is necessarily based on prior literature rather than on data presented in the study. Given the complexity of the circuits involved in integrating internal state, reward, social context, and vigilance, the current work should be viewed as providing a strong behavioral and conceptual framework rather than direct insight into underlying neural mechanisms.

We fully agree that the proposed neural mechanisms remain speculative and that the circuits involved in integrating internal state, reward, and social context are likely far more complex. We have revised the manuscript to acknowledge this limitation.

Methodologically, the behavioral paradigm is well suited for studying escape decisions in socially housed animals, and the machine learning based classification of defensive responses is a clear strength. The computational model provides a useful formalization of how threat level, reward level, and vigilance interact and may be valuable for other laboratories studying escape, approach avoidance, or conflict situations, particularly as a way to classify behavioral outcomes after pose estimation. More generally, the work will be of interest to the neuroethology community for its detailed characterization of escape behavior under naturalistic conditions.

Given the ethological nature of the study and the high inter individual variability reported by the authors, clarity and precision in the methods are especially important for reproducibility. While the revised manuscript addresses many earlier concerns, some aspects remain slightly difficult to follow. For example, the main text states that animals were not water deprived to avoid differences in internal state, whereas parts of the methods describe conditions in which animals were water deprived, suggesting that internal state manipulation may differ across experiments. Clearer separation and explanation of these conditions would further strengthen confidence in the work.

To improve clarity, we have revised the Methods section to clearly distinguish between experimental conditions that involved water deprivation and those that did not.

Overall, this study provides a rich and thoughtful analysis of how reward level and social hierarchy modulate defensive behavior through changes in vigilance. It offers a useful conceptual advance for thinking about escape behavior in naturalistic settings and lays a solid foundation for future work aimed at linking these behavioral states to underlying neural circuits.

Reviewer #2 (Public review):

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

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

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

We agree that reaction time can be influenced by multiple factors, including stimulus strength. Consistent with this, reaction times (i.e. latencies to flee) were substantially shorter under high-contrast conditions (Figure 3E). However, even under the same high-contrast condition, reaction times were significantly shorter in the water condition compared to the no-reward condition, suggesting that other factors such as vigilance may contribute.

Upward-directed attention includes rearing, up-stretching, and upward head orientation, which will be clarified in the Method section. To address concerns about statistical validity, we will quantify these behaviors across the first 10 trials rather than limiting the analysis to the first two.

As for the dominance-related results, we interpret them as reflecting both enhanced vigilance and reduced reward-seeking behavior. Time spent in the reward zone is not a measure of vigilance but an indicator of reward-seeking motivation. We will clarify this in the revised manuscript.

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

In Figure 3B, the difference between water and sucrose conditions did not reach statistical significance (p = 0.08). We plan to collect additional data to determine whether this is due to limited statistical power. It is also possible that some behavioral readouts are more sensitive to the differences between water and sucrose conditions. For example, Figure 3F shows that escape speed was significantly higher in the sucrose than in the water condition under high-contrast stimulation.

Thank you for pointing this out. To control for the potential confounds related to internal state, mice were not water-deprived under any of the three conditions in Figures 3A-3H. We will clarify this in the main text and Methods. For Figures 3I-3M, which compare decision-making under no-reward and water conditions, we will conduct additional experiments using non-deprived mice in the water condition.

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

Hiding latency was defined as the time from stimulus onset to the animal’s arrival at the safe zone. Reaction time was quantified as the latency to flee, measured from stimulus onset to the initiation of the first flight state. The flight state was defined as locomotion exceeding 10 cm at a speed greater than 10 cm/s. Distance fled was defined as the distance covered between stimulus onset and offset for all trials. However, in trials classified as no reaction or freezing, this measure does not accurately reflect escape behavior. We will therefore rename it as distance under threat to better capture its meaning. The reward zone was defined as the region within 15 cm of the reward port at the end of the arena. Duration in the reward zone was measured as the time spent within this region during the 20 seconds following stimulus onset. In Figure 4E, the percentage of time spent in the reward zone was calculated relative to the total time the mouse remained in the arena during the 2-hour social session.

All definitions and additional details on behavioral quantification will be included in the revised Methods section.

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

We appreciate the comment and agree that further clarification is needed. We will provide a more detailed description of the model fitting procedure in the revised Methods section. Specifically, the drift rate parameter (r), which reflects the perceived reward value, was constrained to zero in the no-reward condition. To enable statistical comparison across conditions, we will report uncertainty measures for all fit parameters.

Comments on the revised manuscript:

The manuscript has been revised and improved significantly by the addition of methodological details and new analysis. I remain, however, unconvinced by the argument that increased vigilance in the presence of reward leads to heightened escape behaviour.

In response to my criticism that the work does not measure vigilance directly, the authors have included measures of foraging interval and foraging speed, which they state are "two direct behavioral analyses of vigilance". I disagree - like reaction time, foraging speed and foraging interval can be modulated, for example, by changes in threat sensitivity. Increased threat sensitivity comes with diverse behavioral changes that may well include increased vigilance, but foraging interval and foraging speed can certainly change without the animal expressing increased vigilance behaviors. A bigger issue I still have though, is with the conclusion that the presence of reward increases "direct escape behaviors". Comparing the no reward, water and sucrose groups indeed shows a difference (which is now clear after the split into early and late phases), but the issue is that these are different mice. As the text is written, is sounds like introducing reward will acutely increase escape. But if we look at the raw data show in Figure 2C, what I think is happening is that the presence of reward is decreasing habituation to the stimulus. The data for trials 1 and 10 in the three conditions show this - there is habituation with no reward (reaction times are all shifting to the right), a bit less with water and very little with sucrose. This is interesting in its own right and we can speculate why it might be happening, but I think this is conceptually different from what the authors are proposing.

We agree that vigilance is not directly observable as a single variable. Our intent was not to claim that foraging speed and foraging interval provide a direct measure of vigilance, but rather to suggest that they may serve as indirect behavioral correlates.

We also considered an alternative interpretation: these two measures could reflect perceived reward value under high-threat conditions across distinct reward types. If that were the case, animals would be expected to exhibit shorter intervals and faster speeds across no reward, water, and sucrose conditions. However, our data do not support this interpretation (Figures 3L and 3M), suggesting that these measures are more likely correlated with vigilance. 

Furthermore, it is unlikely that changes in foraging interval and speed are driven by altered threat sensitivity, as animals could not see the threat during most of the foraging bout and only encountered it at the end.

Regarding the conclusion that the presence of reward increases direct escape behaviors, our interpretation is that increased reward value reduces habituation, thereby maintaining higher vigilance during the late phase. This was discussed in the second-to-last paragraph of the "Economic and social modulations of innate decision-making under threat" subsection in the Discussion.

Reviewer #3 (Public review):

Male mice were tested in a classic behavioral "flee the looming stimulus" paradigm. This is a purely behavioral study; no neural analyses were done. Mice were housed socially, but faced the looming stimulus individually, using an elegant automated tunnel (see videos for clarity).

The additional changes made to the paper clarify the work done. While there are some limitations (male mice, weird stimulus), the general results are interesting and a valuable addition to the experimental literature. The main claim of the paper is that the different rewards (none, water, sucrose) did not change the escape properties early in learning, but did late, particularly that in the late (already experienced) conditions, reward value (assuming sucrose > water > no reward) interacted with the salience of the looming stimulus (light gray, dark gray). (Panels 3D, 3G, 3K, 3N).

For readers, I want to note that one of the most interesting results is actually in Figure S2, where they find that a looming stimulus behind the mouse still makes a mouse run to the nest. In these conditions, the mouse runs past the looming stimulus to get to safety! (I also do love the video of the mouse running around the barriers like a snake to get home.)

I have a few minor clarification questions and a few notes that I think would be useful additions for authors and readers to think about.

Dominance: What does the mouse social science literature say about the "test tube" test? What can we conclude from this test? This would be useful when trying to understand what is causing the dominance/submissive difference in responses. Figure 4 shows that the dominant mice are more risk-averse than the submissive mice. Is "dominance" in the test-tube actually a measure of risk-seeking? Is the issue that the submissive mice don't think they can get back to the food-site easily, so they are less willing to sacrifice the current (if dangerous) foraging opportunity? Is the issue that the submissive mice can't get back to the nest? As I understand it, the nest was always available to all the mice, so I suspect inability to get to the nest is an unlikely hypotheses. Is the issue that the submissive mice also don't feel safe in the nest?

The tube test is a widely used assay in the rodent social behavior literature to assess dominance hierarchies, operationally defined by the ability of one animal to force its opponent to retreat from a narrow tube. Importantly, this assay does not directly measure risk-seeking or anxiety-related traits, but rather competitive outcomes during social conflict. Furthermore, our data indicate that the behavioral responses of subordinate mice to looming stimuli are primarily driven by the visual threat itself rather than by social avoidance. This point was elaborated in the second paragraph of the “Social modulation of innate decision-making” subsection in the Results section.

Limitations of the study: There is an acknowledged limitation to male mice, and the limitations of the small data sets that are typical of such experiments. In addition, however, it is also worth noting the strangeness of the looming stimulus, which is revealed clearly in the videos. The stimulus is a repeating growing circle, growing in a single location within the environment. The stimulus repeats 10 times, once per second. This is not what an attacking hawk or owl would look like. (I now have this image of an owl diving down, and then teleporting up and diving down again.) Note - I am fine with this stimulus. It produces an interesting experiment and interesting results. I do not think the authors need to change anything in their paper, but readers need to recognize that this is not a "looming predator".

These "limitations" are better seen as "caveats" when folding these results in with the rest of the literature that has gone before and the literature to come. (Generally, I do not believe that science works by studies making discoveries that change how we think about problems - instead, science works by studies adding to the literature that we integrate in with the rest of the literature.) Thus, these caveats should not be taken as problems with the study or as fixes that need to be done. Instead, they are notes for future researchers to notice if differences are found in any future studies.

Thus, my only suggestion is that I think authors could write a more careful paper by using the past and subjunctive tense appropriately. Experimental observations should be in past tense, as in "the influence of reward was context-dependent and emerged in the late phase" instead of "the influence of reward is context-dependent and emerges in the late phase" - it emerged in the late phase this once - it might not in future experiments, not due to any fault in this experiment nor due to replicability problems, but rather due to unexpected differences between this and those future experiments. At which point, it will be up to those future experiments to determine the difference. Similarly, large conclusions should be in the subjunctive tense, as in "these data suggest that threat intensity is likely to be the primary determinant of decision making" rather than "threat intensity is the primary determinant of decision making", because those are hypotheses not facts.

We thank the reviewer for the helpful suggestions and have revised the Abstract accordingly.

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

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

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

Weaknesses:

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

We agree that these details are essential and have clarified them in the Methods. When the door system operated normally, only one mouse was allowed in the arena during looming exposure. Specifically, when all mice were in the nest, the nest-tunnel door was open and the tunnel-arena door was closed. Once a single mouse entered the tunnel, as detected by an OpenMV camera, the nest-tunnel door closed and the tunnel-arena opened, ensuring that only that mouse could enter the arena.

Habituation was conducted over two days. On day 1, five mice were placed together in the nest for 30 minutes with all doors closed. Each mouse was then placed individually in the nest and allowed to freely explore the arena for 10 minutes under normal door operation. Finally, all mice were returned to the nest with all doors open and allowed for free exploration for 2 hours. On day 2, each mouse was placed individually in the nest and given an additional 1 hour of exploration under normal door operation.

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

We observed substantial inter-individual variability in habituation to looming stimuli, with a sharp decline in defensive responses over the first few trials followed by more gradual changes. To account for this, we segmented trials for each animal into two phases: an early rapidhabituation phase and a later stable phase. Analyzing these phases separately revealed that threat intensity dominates behavior in the early phase, whereas both threat and reward significantly influence behavior in the late phase. These results are now presented in revised Figures 2 and 3. Analyses restricted to first trials are included in Figure S5.

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

As noted above, we have re-analyzed our data to account for learning effects.

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

We have substantially revised the modeling analysis. The model is now fitted to behavioral data from the late phase and used to predict outcomes across additional conditions, including the early phase behavior and rank-dependent behavioral differences. The model successfully captures behavioral patterns across these conditions, supporting its predictive value beyond descriptive fitting.

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

To support the interpretation of increased vigilance with reward under high-threat conditions, we analyzed additional behavioral measures beyond latency to flee. Rewarded mice showed longer foraging interval and slower foraging speed, both consistent with elevated vigilance (Figures 3L and 3M).

To address the alternative explanation that subordinate mice may remain in the arena due to restricted nest access, we compared arena occupancy before, during, and after looming exposure. Although subordinates spent more time in the arena before looming, this difference disappeared during and after looming exposure (Figures 4C). Moreover, dominant and subordinate mice were

equally likely to flee to the nest during escape trials. These findings rule out nest access restrictions as an explanation for the observed rank-dependent differences in defensive behaviors.

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

We have revised the Introduction to incorporate relevant brain regions and neural circuits.

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

We have substantially revised the figures. Results from trial segmentation based on individual habituation are now explicitly presented in Figures 2 and 3, and analyses using only the first trials are provided in Figure S5 to separate initial responses from learning effects.

Regarding the original Figure 4H, we are not entirely certain about the concern. In this panel, we measured time spent in the reward zone, which is defined as the region within 10 cm of the reward port at the end of the arena, not the center of the arena, during looming exposure. Subordinate mice spent significantly more time in the reward zone than dominant mice. We have further clarified this in the revised manuscript.

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

We observed substantial individual variability in both dominant and subordinate mice, even on the first trial (Figure S7). Paired dominant–subordinate comparisons were used to isolate rankdependent effects.

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

Robust looming-evoked defensive responses have been reported in both group- and singlehoused mice (Yilmaz and Meister, 2013, Lenzi et al., 2022), although single-housed mice habituate more rapidly. We have now discussed the potential interactions between housing conditions, social rank, and habituation in defensive behaviors in the revised manuscript.

Reviewer #2 (Public review):

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

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

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

We agree that reaction time can be influenced by multiple factors, including stimulus strength. Consistent with this, reaction times (i.e. latencies to flee) were substantially shorter under highcontrast conditions. However, even under the same high-contrast condition, reaction times were significantly shorter in the reward conditions compared to the no-reward condition, suggesting that other factors such as vigilance may contribute.

Regarding the measurement of vigilance, in addition to the latency to flee, we analyzed two additional behavioral measures related to vigilance. First, we examined the foraging interval. Our hypothesis was that more vigilant animals would wait longer before re-entering the reward zone following threat exposure. Consistent with this prediction, mice under sucrose and water reward conditions showed significantly longer foraging intervals than those under no-reward conditions (Figure 3L). Second, we analyzed the foraging speed as mice approached the reward. Increased vigilance should lead to more cautious and therefore slower movements. Our results support this, as mice moved more slowly towards the reward under sucrose conditions (Figure 3M). Taken together, these three measures consistently indicate that mice exhibit increased vigilance under sucrose reward in high-threat conditions.

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

Our new analysis, which segments behavior into an early adaptive phase and a late stable phase, reveals a statistically significant difference between water and sucrose rewards in the late phase (Figure 3H), supporting a graded effect of reward value.

To control for the potential confounds related to internal state, mice were not water-deprived in all reward conditions. We have clarified this in the revised manuscript.

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

Hiding latency was defined as the time from stimulus onset to the animal’s arrival at the safe zone. Reaction time was quantified as the latency to flee, measured from stimulus onset to the initiation of the first flight state. The flight state was defined as locomotion exceeding 10 cm at a speed greater than 10 cm/s. Distance fled was defined as the distance covered between stimulus onset and offset for all trials. However, in trials classified as no reaction or freezing, this measure does not accurately reflect escape behavior. We will therefore rename it as distance under threat to better capture its meaning. The reward zone was defined as the region within 10 cm of the reward port at the end of the arena. Duration in the reward zone was measured as the time spent within this region during the 20 seconds following stimulus onset. In Figure 4E, the percentage of time spent in the reward zone was calculated relative to the total time the mouse remained in the arena during the 2-hour social session.

All definitions and additional details on behavioral quantification have been included in the revised Methods section.

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

We have provided a detailed description of the model fitting procedure in the revised Methods section. Specifically, the reward-value parameter (r) was constrained to zero in the no-reward condition. We have plotted how the overall loss varies with differeent parameters (Figure S9).

Reviewer #3 (Public review):

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

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

Regarding the interpretation of stimulus contrast as a proxy for threat level, we agree it is crucial to distinguish improved detection from heightened threat perception. To address this, we examined not only latency to flee but also escape distance and peak escape speed, two measures that reflect the intensity of the defensive response. If contrast only influenced detection, we would expect differences in latency but not in escape distance or speed. All three measures differed significantly across contrast conditions, supporting the interpretation that high-contrast stimuli are perceived as more threatening rather than simply more detectable. Furthermore, manual review of "no response" trials confirmed reliable detection in both conditions, with only three potential "missed" trials out of 117 under low contrast (Figure S3B). We have included this discussion in the revised manuscript.

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

Because our model is fit to the variance of latency distributions, it cannot be applied to singletrial data. Instead, we analyzed how decisions and latencies vary as functions of the fitted threat gain and reward value parameters (Figures 5G and 5H). We have also introduced a simplified deterministic model to further elucidate the decision-making process.

Regarding the influence of distance to the threat, we conducted additional experiments, presenting the looming stimulus at the end of the arena when the mouse was at different distances from it (Figures S2C–G). We found that as the prey-threat distance increased, mice showed less direct escape behavior, with longer latencies to flee and slower escape speeds. This is consistent with the predatory imminence continuum theory (Fanselow and Lester, 1988), which describes graded defensive behaviors tuned to perceived threat level.

Regarding the influence of distance to safety, our data indicate that it did not significantly affect defensive responses (Figures S2H and S2I). To test this further, we introduced barriers that lengthened the return path to the safe zone. We found that defensive decisions were not correlated with the distance to the safe zone (Figures S2J and S2K), suggesting that once a threat is detected, animals prioritize escape initiation over evaluating the exact path to safety.

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

We have expanded our analysis of vigilance. In addition to escape latency, we examined the foraging interval and foraging speed. We hypothesized that more vigilant animals would wait longer before re-entering the reward zone following a threat and would approach the reward more slowly. Consistent with this prediction, mice in the sucrose- and water-reward conditions exhibited significantly longer foraging intervals and slower foraging speeds compared to those in the no-reward condition (Figures 3M and 3N). Together, these three measures consistently demonstrate that mice display heightened vigilance under high-threat, high-reward conditions.

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

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

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

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

We have substantially revised the manuscript to contextualize our findings within the extensive literature on defensive behavior and decision-making. The revised Introduction and Discussion now integrate key theoretical frameworks, such as the predatory imminence continuum, and cite relevant work on active avoidance and other "flee the predator" paradigms (e.g., the Robogator task).

We have also incorporated perspectives from neuroeconomics and motivational conflict, including literature on sequential foraging, delay-discounting tasks, and relevant rodent studies. Furthermore, we now discuss the potential contributions of specific brain regions, including the superior colliculus and the amygdala, to the economic and social modulation of innate defensive decisions in response to visual threats.

Recommendations for the authors:

Reviewing Editor Comments:

These additional recommendations are generally consistent and overlapping across reviewers, particularly Reviewer #1 and 2, so it is advisable to undertake these changes/additions.

Reviewer #1 (Recommendations for the authors):

(1) Experimental methods and trial structure need clarification: It is often unclear how many trials were included per condition, per mouse, and whether the key behavioral effects (especially reward-related changes) were observed early in the session or after repeated stimulus exposure. For example, in several reward-related plots (e.g., Figure 3), it is not specified whether results are driven by early or later trials. Since the authors themselves report rapid learning of the looming stimulus (habituation), it is critical to state how many trials were included in each comparison, and to analyze whether effects hold on the first exposure and not the rest. Otherwise, conclusions about value-based behavior are hard to separate from learning effects, which may also differ between individuals. Specifically, the methods section is vague and hard to follow.

We have substantially expanded the Methods section with additional details to improve clarity.

To account for individual variability in habituation to the looming stimulus, we segmented trials for each animal into early and late phases. We demonstrate that threat level is the dominant factor driving behavioral responses in the early phase, while both threat level and reward condition shape behavior in the late phase. We have substantially revised Figures 2 and 3 to reflect these changes.

(2) Add a summary of experimental design: A table or schematic summarizing the trial structure, experimental groups, reward/threat conditions, and the timeline of exposures would greatly improve clarity.

We have added a schematic to Figure 2 summarizing the trial structure, experimental groups, reward and threat conditions, and the overall timeline.

(3) Replot key results using only the first trial per mouse: This would allow readers to assess the first (not learned) responses and help control for habituation/suppression.

We have replotted behavioral results using only the first trial from each mouse and included these analyses in Figure S5. These results confirm that threat level is the dominant factor driving the initial response to looming stimuli.

(4) The model needs stronger justification and predictive value: As it stands, the model primarily fits the existing data and does not offer new insights beyond what is already evident from the behavioral results.

Important findings, such as social hierarchy effects and habituation dynamics, are not captured in the model, reducing its relevance to the full dataset.

The drift-diffusion framework is widely used, and in this implementation appears to have been adjusted post hoc to fit the observed data rather than generating new conceptual advances. No comparison with simpler models is included. Without testing simpler or alternative models, it is not clear whether the added complexity is necessary or justified.

Use the model to generate and test predictions: to increase the model's contribution, the authors could simulate new conditions. Suggested experiments include:

a) Predicting escape probability and latency at intermediate threat intensities to test whether behavior shifts gradually or abruptly.

b) Using the model's habituation parameters to predict changes in escape behavior over repeated exposures.

c) Adjusting vigilance or threat gain parameters to simulate dominant versus subordinate animals, and comparing model predictions to actual behavioral differences based on social rank.

We have substantially revised the modeling section to address these concerns. The updated model is now fitted to behavioral data from the late phase of the reward–threat experiments and used to generate predictions for the early phase and for rank-dependent behavioral differences.

The model accurately captures behavioral patterns across these conditions, demonstrating predictive power beyond descriptive fitting. Accordingly, we have removed the habituation component. Furthermore, we have introduced a simplified deterministic model in the revised manuscript to further understand the decision-making process.

(5) Clarify housing and arena access conditions: It is unclear from the text whether all mice are in the nest during looming presentations and whether only one mouse is in the arena during the stimulus. This is important for understanding the social context of each trial and should be explained in the main text and methods.

We have clarified this point in the Methods section. Under normal door operation, only one mouse was allowed in the arena during looming exposure. Specifically, when all mice were in the nest, the nest-tunnel door was open and the tunnel-arena door was closed. Once a single mouse entered the tunnel, as detected by an OpenMV camera, the nest-tunnel door closed and the tunnel-arena opened, ensuring that only that mouse could enter the arena.

(6) Alternative interpretation of subordinate behavior: differences in area coverage and time in the reward zone may not reflect reduced vigilance, but rather avoidance of dominant mice. Subordinates may remain in the open arena to avoid conflict. The authors do not provide evidence distinguishing between these interpretations, and this should be addressed.

To address the alternative explanation that subordinate mice may remain in the arena due to restricted nest access, we compared arena occupancy before, during, and after looming exposure (Figure 4C). Before looming exposure, subordinate mice spent significantly more time in the arena, consistent with the idea that they may perceive a social threat from the dominant mouse in the absence of any external threat. However, this difference disappeared during and after looming exposure. This shift suggests that the presence of an external threat alters the social dynamic, reducing the influence of dominance on nest access.

To further assess whether dominant mice blocked subordinate access to the nest during threatdriven escapes, we analyzed the fraction of escape trials in which mice returned to the nest (Figure 4D). We found no significant difference between dominant and subordinate mice, indicating that dominant mice did not restrict nest access during these trials. Importantly, rank differences in reward-zone occupancy cannot be explained by nest exclusion, as mice do not need to return to the nest when escaping the threat—they can flee directly to the safe zone. Thus, nest access limitations do not account for the observed rank-dependent patterns.

We agree with the reviewer that reward-zone occupancy should not be interpreted as reduced vigilance in subordinate mice; instead, it likely reflects higher perceived reward value. The manuscript has been revised accordingly.

(7) Address why robust looming responses were observed in group-housed mice: previous studies often require single housing to elicit strong defensive responses. The authors should explain why their setup yields robust results in group-housed animals and whether housing conditions may interact with dominance or habituation.

Looming exposure elicits robust defensive behaviors in both group- and single-housed mice (Yilmaz and Meister, 2013, Lenzi et al., 2022), with single-housed animals habituating more quickly to the stimulus (Lenzi et al., 2022). We have now discussed how housing conditions may interact with social rank and habituation to shape defensive behaviors in the revised manuscript.

For the social-rank experiments, we intentionally co-housed dominant and subordinate mice to maintain a stable hierarchy. This choice was motivated by two considerations. First, our goal was to investigate how social rank modulates defensive responses under ethologically relevant conditions, where mice naturally live in groups. Single housing would remove this social context. Second, singly housing mice can destabilize or eliminate rank relationships, making it difficult to interpret rank-dependent behavioral differences.

(8) Add analysis of individual variability: trial-by-trial variability or stable behavioral tendencies in individual animals are not explored. This could explain part of the variation currently attributed to social rank.

We have analyzed individual variability in both dominant and subordinate mice. We observed substantial variability across all behavioral measurements for each group (Figure S7). To attribute the observed behavioral differences to social hierarchy rather than to other individual traits, we conducted paired comparisons between dominant and subordinate mice (Figure 4).

(9)  Improve figure labeling and readability: some plots are ambiguous in terms of whether rows represent trials or animals. Overlapping points obscure the data in several figures, for example, Figure 3H, sucrose is n=4?- consider using jittered scatter plots, boxplots, or individual traces to improve clarity. Also same Figure axis Y is missing an 'e'.

We have revised figures to improve clarity and corrected the typos.

(10) Avoid overinterpretation of causal explanations: Statements such as "reward increases vigilance due to evolutionary pressure" or that "subordinates are less vigilant" go beyond what the current data can demonstrate and should be rephrased more cautiously.

We have revised the manuscript to tone down the statement.

Reviewer #2 (Recommendations for the authors):

(1) Provide much more extensive methodological details on analyses and model fitting

We have thoroughly revised the Methods section to provide extensive detail on both behavioral analyses and computational modeling, as outlined in our responses to points (3) and (4) of the Public Review.

(2) Perform experiments or analyses that directly measure vigilance, if vigilance is to remain as a key explanation for the data.

As detailed in our response to point (1) of the Public Review, we have supplemented the escape latency measure with two direct behavioral analyses of vigilance: foraging interval and foraging speed. This multi-metric approach robustly supports the interpretation of heightened vigilance.

(3) Provide extra evidence for an effect of reward value, as opposed to the presence or absence of reward. Control for differences arising from the water deprivation state by performing the no reward condition experiments in water-deprived mice.

All behavioral data in the reward–threat experiment were collected on normal (non-deprived) mice (Figures 2 and 3), which have been clarified in the revised manuscript. We have reanalyzed the data by segmenting trials into early and late phases for each animal. In the late phase, under low-threat conditions, the effect of reward value is reflected in significant differences between water and sucrose in terms of escape distance and time spent in the reward zone (Figures 3I and 3J). Under high-threat conditions, the reward value effect is reflected in significant differences in latency to flee and peak escape speed (Figures 3K and 3N).

(4)  Using drift rate to describe the "r" variable is confusing because the drift rate of the drift diffusion process is also determined by terms alpha, beta, and h-terms.

We have termed “r” as the reward value in the revised manuscript.

Reviewer #3 (Recommendations for the authors):

(1) I would tone down some of the extreme statements about the problems of previous experiments (such as that most decision-making is on 2AFC). Lots of people do decision-making in serial foraging, fleeing, and other behavioral tasks. The classic Morris water-maze or Barnesmaze are decision-making tasks that aren't 2AFC. Serial foraging tasks, such as the Restaurant Row task aren't 2AFC. And, actually, lots of mouse behavior tasks are deciding when to stop on a treadmill for a reward. And, for that matter, your task isn't all that "realistic" - mice aren't evolved to flee looming disks, they are evolved to flee hawks and owls. This doesn't invalidate your task at all. I just recommend making it about your work in a positive way rather than others in a negative way.

We have revised the manuscript to adopt a more positive framing of our work.

(2) I also don't think there's much use in bringing in crayfish in a mouse task. Spend your time connecting to the other rodent data (mice and rats) instead.

We agree and have revised the manuscript accordingly, focusing our discussion on relevant rodent literature to provide a more appropriate context for our findings.

Minor concerns:

(1) The authors use the term "cognitive control" without making clear what they mean. In general, the authors seem to have a view on decision-making as either being "reflexes" or "cognitive control". This is a very outdated perspective. Modern perspectives include multiple decision-making systems competing, separating these based on their computational properties, such as planning, procedural, instinctual, and, yes, reflexive. Current views on the kinds of behaviors they are discussing generally see fleeing as a transition from reflexive (tonic immobility, freezing) and instinctual responses (freezing, fleeing) to deliberative (anxiety) and procedural (habit). The authors might take a look at the recent Calvin and Redish (2025) paper for some ideas on this.

We appreciate the reviewer’s insight regarding the term “cognitive control.” In our study, we used this term to emphasize that defensive responses to looming threats are not purely reflexive. Mice exhibit four distinct types of defensive decisions within a short time window, and these decisions are systematically modulated by reward value and social rank. Notably, reward modulation is bidirectional: high reward suppresses defensive responses under low-threat conditions but enhances them under high-threat conditions, indicating that animals integrate multiple sources of information rather than relying solely on instinctive mechanisms.

We did not observe mid-trajectory aborts in mice, as reported in rats by Calvin & Redish (2025). This difference may reflect species-specific behavior or the nature of the threat: our looming stimulus is purely visual and non-harmful, whereas the robotic predator in their study presents a physical threat. We have revised the Discussion to clarify our use of “cognitive control” and to incorporate these perspectives.

(2) Only male mice were used. This limits the conclusions that can be drawn.

We acknowledge the limitation of using only male mice and have discussed this limitation in the revised manuscript.

(3) Did the authors observe darting behavior? (Gruene...Shansky 2015).

We did not observe darting behavior, characterized by rapid movement, as reported during inescapable fear conditioning. In our experiment, the mice consistently escaped towards the nest, in most trials, ran directly to the nest without stopping. Occasionally, under low contrast conditions, mice paused once or twice but never moved towards the reward.

(4) How was only one mouse allowed into the linear arena at a time?

When all mice were in the nest, the nest-tunnel door was open while the tunnel-arena door remained closed. When a single mouse entered the tunnel, as detected by the RFID and OpenMV camera system, the nest-tunnel door closed and the tunnel-arena door opened, allowing only that mouse to enter the arena. We have clarified this protocol in the Methods section.

(5) I would like to see more extensive analyses of the animal's responses as a function of distance to the threat (as per Fanselow and Lester 1988).

As detailed in our response to the public review, we conducted new experiments analyzing behavior as a function of prey–threat distance. The finding that defensive responsiveness decreases with increasing prey–threat distance is now presented in Figures S2C–G and discussed in the context of the predatory imminence continuum.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

In this manuscript, the authors report that GPR55 activation in presynaptic terminals of Purkinje cells decrease GABA release at the PC-DCN synapse. The authors use an impressive array of techniques (including highly challenging presynaptic recordings) to show that GPR55 activation reduces the readily releasable pool of vesicle without affecting presynaptic AP waveform and presynaptic Ca²⁺ influx. This is an interesting study, which is seemingly well-executed and proposes a novel mechanism for the control of neurotransmitter release. However, the authors' main conclusions are heavily, if not solely, based on pharmacological agents that most often than not demonstrate affinity at multiple targets. Below are points that the authors should consider in a revised version.

We are happy to hear the encouraging comments from this reviewer, and thank for pointing out the important issues including the previous study design depending only on pharmacological agents. To address these, we have performed additional experiments, as detailed below.

Major points:

(1) There is no clear evidence that GPR55 is specifically expressed in presynaptic terminals at the PC-DCN synapse. The authors cited Ryberg 2007 and Wu 2013 in the introduction, mentioning that GPR55 is potentially expressed in PCs. Ryberg (2007) offers no such evidence, and the expression in PC suggested by Wu (2013) does not necessarily correlate with presynaptic expression. The authors should perform additional experiments to demonstrate the presynaptic expression of GPR55 at PC-DCN synapse.

We completely agree with the reviewer in that our previous manuscript lacked the reliable information regarding presynaptic expression of GPR55 at PC boutons.

To clarify the localization, we first tried immunostaining of GPR55 using commercially available antibodies, but unfortunately they did not provide clear labeling of neurons and also even in GPR55-transfected HEK cells (used as positive control). Thus, we gave up the direct immunostaining. Alternatively, we attempted to label PC axonal boutons by GPR55-targeting dye together with a complementary strategy based on gene knock-down. Specifically, we used T1117, a fluorescent derivative of AM251 which is a GPR55 ligand used in the manuscript, and clear fluorescent signals were evident at GFP-labeled PC terminals. Still, by itself it was not clear whether the labeling was mediated by association with GPR55. Therefore, we also attempted to specifically suppress gene expression of GPR55 using CRISPR/Cas9-mediated genome editing in PCs, based on acute DNA micro-injection of plasmids into nuclei of PCs to express gRNAs targeting GPR55 together with Cas9. As a result, 5 days after the knock-down, T1117 labeling at axon terminals was reduced by ~50% compared to Cas9-alone controls. All these data are now shown in new Figure 2, and explained in the text p5-6, lines 141-159. Further, the reduction of GPR55 expression abolished the AM251-mediated reduction of vesicular exocytosis, as shown in new Figure 3D, E.

Taken together, these results essentially convince our main conclusions by strongly suggesting that GPR55 is present at PC axon terminals, where it negatively regulates the exocytosis upon activation by AM251.  

(2) The authors' conclusions rest heavily on pharmacological experiments, with compounds that are sometimes not selective for single targets. Genetic deletion of GPR55 would be a more appropriate control. The authors should also expand their experiments with occlusion experiments, showing if the effects of LPI are absent after AM251 or O-1602 treatment. In addition, the authors may want to consider AM281 as a CB1R antagonist without reported effects at GPR55.

We thank the reviewer for pointing out these important issues. First, as noted above to confirm the presence of GPR55 at axon terminals of PCs, we performed genetic deletion of GPR55 using CRISPR/Cas9 system. In PCs co-expressing Cas9 and two gRNAs targeting the ligand-binding domain of GPR55, AM251 failed to suppress the exocytosis at PC boutons, together with decreased T1117 labeling. Therefore, the idea that GPR55 negatively regulates transmitter release at PC boutons has now been strengthened. The new data is shown in Figure 3D and E, and explained in the text p6, lines 173-178.  

As suggested, we also carried out the occlusion experiments with LPI and AM251. First, LPI similarly reduced the readily releasable pool (RRP) size as AM251 did. Then, applied together, LPI and AM251 did not further reduce the RRP size compared with the effect by either compound alone. Thus, LPI and AM251 seem to act through the same pathway, consistent with the idea for role of GPR55 activation. The data is shown in new Figure 5—figure supplement 1 and explained in the text, p7-8, lines 215-221.

Regarding another point suggested by the reviewer, we applied AM281 and observed no effect on transmission at the PC–target neuron synapses (shown in new Figure 1F and I; explained in the text p5, lines 117-123), indicating that the effect of AM251 is likely to be mediated by GPR55, but not by CB1R.

Taken together, our additional experiments based on genetic and pharmacological experiments have consolidated our conclusion that GPR55 suppresses the presynaptic neurotransmitter release in PC boutons.

(3) It is not clear how long the different drugs were applied, and at what time the recordings were performed during or following drug application. It appears that GPR55 agonists can have transient effects (Sylantyev, 2013; Rosenberg, 2023), possibly due to receptor internalization. The timeline of drug application should be reported, where IPSC amplitude is shown as a function of time and drug application windows are illustrated.

Thank you for suggesting the better presentation of data. Accordingly, we have re-organized figures showing time course of changes in IPSCs before and after the drug application (new Figure 1 and 4; p4, lines 94-97; p5, lines 110-115; p7, lines 193-197). The current data presentation clearly shows that the effect of AM251 becomes evident in a few minutes after application, and somehow reaches a saturated level.

(4) A previous investigation on the role of GPR55 in the control of neurotransmitter release is not cited nor discussed (Sylantyev et al., (2013, PNAS, Cannabinoid- and lysophosphatidylinositolsensitive receptor GPR55 boosts neurotransmitter release at central synapses). Similarities and differences should be discussed.

We are really sorry for failing to adequately discuss this important work in our previous manuscript, and deeply appreciate the reviewer for pointing this out. We have now cited and discussed the work by Sylantyev et al. (2013), in the text (p12, lines 380-389), as following:

‘Pioneering studies clarified an important role of GPR55 in synaptic transmission at hippocampal excitatory synapses, demonstrating presynaptic enhancement of glutamate release presumably by elevating the cytoplasmic residual Ca²⁺ via release from intracellular stores (Sylantyev et al., 2013; Rosenberg et al., 2023), in contrast to the suppression of release in our observation. The lack of positive modulation of AP-triggered release through residual Ca²⁺ in PC terminals might be due to abundant amount of potent Ca²⁺ buffer calbindin (Fierro and Llano, 1996). Indeed, increased vesicular fusion only for the AP-insensitive spontaneous vesicular release (as mIPSCs) was observed upon the IP₃-mediated Ca²⁺ release from internal store (Gomez et al., 2020). Thus, minimal sensitivity of AP-triggered release to residual Ca²⁺ in PC boutons would underlie the distinct effects of GPR55 activation at the presynaptic side.’  

Minor point:

(1) What is the source of LPI? What isoform was used? The multiple isoforms of LPI have different affinities for GPR55.

Thank you for letting us know about the lack of important information in the previous manuscript. In our experiments, we used a soybean-derived LPI mixture containing approximately 58% C16:0 and 42% C18:0 or C18:2 species. According to Brenneman et al. (2025), these isoforms show moderate or strong effects in cultured DRG neurons, whereas the C20:4 isoform, reported to promote neuroinflammatory signaling, was contained only at very low levels. We have added this information to the revised manuscript and briefly discussed the influence of different LPI isoforms on the physiological outcomes of GPR55 activation (p5, lines 127-131; p15, lines 493-496).

Reviewer #2 (Public review):

Summary:

This paper investigates the mode of action of GPR55, a relatively understudied type of cannabinoid receptor, in presynaptic terminals of Purkinje cells. The authors use demanding techniques of patch clamp recording of the terminals, sometimes coupled with another recording of the postsynaptic cell. They find a lower release probability of synaptic vesicles after activation of GPR55 receptors, while presynaptic voltage-dependent calcium currents are unaffected. They propose that the size of a specific pool of synaptic vesicles supplying release sites is decreased upon activation of GPR55 receptors.

Strengths:

The paper uses cutting-edge techniques to shed light on a little-studied, potentially important type of cannabinoid receptor. The results are clearly presented, and the conclusions are for the most part sound.

We feel very happy to see the positive comments from the reviewer.  

Weaknesses:

The nature of the vesicular pool that is modified following activation of GPR55 is not definitively characterized.

We agree with the reviewer in that our data cannot fully address the changes of vesicle pools caused by GPR55. As detailed in responses to comments in ‘Recommendations for the authors’ from the reviewer, we have added explanation and discussion in the main text of the revised manuscript.

Reviewer #3 (Public review):

Summary:

Inoshita and Kawaguchi investigated the effects of GPR55 activation on synaptic transmission in vitro. To address this question, they performed direct patch-clamp recordings from axon terminals of cerebellar Purkinje cells and fluorescent imaging of vesicular exocytosis utilizing synaptopHluorin. They found that exogenous activation of GPR55 suppresses GABA release at Purkinje cell to deep cerebellar nuclei (PC-DCN) synapses by reducing the readily releasable pool (RRP) of vesicles. This mechanism may also operate at other synapses.

Strengths:

The main strength of this study lies in combining patch-clamp recordings from axon terminals with imaging of presynaptic vesicular exocytosis to reveal a novel mechanism by which activation of GPR55 suppresses inhibitory synaptic strength. The results strongly suggest that GPR55 activation reduces the RRP size without altering presynaptic calcium influx.

We thank the reviewer for giving the encouraging comments on our study.

Weaknesses:

The study relies on the exogenous application of GPR55 agonists. It remains unclear whether endogenous ligands released due to physiological or pathological activities would have similar effects. There is no information regarding the time course of the agonist-induced suppression. There is also little evidence that GPR55 is expressed in Purkinje cells. This study would benefit from using GPR55 knockout (KO) mice. The downstream mechanism by which GPR55 mediates the suppression of GABA release remains unknown.

We thank the reviewer for pointing out all of these important issues to be ideally addressed. As detailed in the responses to comments in the ‘Recommendations for the authors’ from the reviewers, we have addressed most of these weak points, and also added careful discussion in the text about the open questions to be solved in the future study.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

This is a high-quality paper that reports novel and interesting results. The authors should consider one main critique, related to Figure 6, as well as a number of minor points.

We thank the reviewer for making very positive assessment of our study. We have carefully considered the main critique regarding presynaptic vesicle pools (related to previous Figure 6), as well as other points, and accordingly revised manuscript.

Main critique:

In Figure 6, it is said that GPR55 locks SVs in a state that is insensitive to VGCCs, based on a series of experiments with synapto-pHluorin. This conclusion is open to several critiques:

The authors' model is shown in the diagram of Figure 6A. In this scheme, it appears as if recycled SVs eventually re-acidify in spite of the presence of bafilomycin, and that they are directed to a location close to the plasma membrane, but away from VGCCs. In fact, there is no evidence that the effects of bafilomycin could be limited in time. And there is a lot of evidence indicating that recycled SVs move back to release sites, close to VGCCs.

We are so sorry for presenting misleading figure panel in the previous Figure 6A. As the reviewer says, the effect of bafilomycin should be expected to last for long, and then the endocytosed vesicles cannot be re-acidified. Now, in new Figure 8A, we have changed the panel for explanation about the experimental situation of vesicles in the presence of bafilomycin. Another insightful point, kindly suggested by the reviewer, regarding the quick recruitment of newly endocytosed vesicles to release sites, is highly related to the interpretation of our data, but is a different issue from the situation explained in new Figure 8A. To avoid confusion, the arrow drawn in the previous version indicating the endocytosed vesicle movement back to the docked situation has been omitted in the new panel, and this critical issue is now carefully discussed in terms of the mechanism of GPR55 action on the release machinery (p15, lines 480-482).

The saturation of the train-induced signals is interpreted as reflecting an exhaustion of SVs initially close to VGCCs or more generally, susceptible to being released following VGCC activation.

In an alternative scenario, saturation occurs because AP trains, or KCl applications, become unable to activate VGCCs. This could occur either because long illumination causes photodamage of VGCCs, or because repeated activation of VGCCs leads to their inactivation. The latter explanation is possible in spite of a publication from the authors' laboratory describing the facilitation of presynaptic VGCCs following paired stimulations in this synapse (Diaz-Rojas et al., 2015).

We agree that it is an important control experiment to demonstrate that Ca²⁺ increase upon repetitive AP trains is intact even during or after the long photo-illumination for imaging. To test this possibility, we have performed additional fluorescent Ca²⁺ imaging at PC varicosities during individual 400-AP trains and also in response to 50 mM KCl following the series of AP trains. Now new data demonstrated that Ca²⁺ influx remains constant across all AP trains (shown in Figure 8— figure supplement 1), arguing against VGCC inactivation or photodamage as a major factor underlying the saturated signal increase in the synapto-pHluorin. We have added explanation regarding this issue in the text p11, lines 327-329.

The authors explain the larger effect of ionomycin compared with AP trains and KCl applications as reflecting a better capacity to increase the bulk calcium concentration. The above proposal for the inactivation of VGCCs offers an alternative explanation, in my view more likely.

As noted above, our newly added Ca²⁺ imaging data clearly showed that individual AP trains induced similar Ca²⁺ influxes during repetitive trials, in line with our original interpretation. In addition, the Ca²⁺ increase by KCl was shown to be more potent and broader in axon terminals and trunks. Nevertheless, the exocytic signal caused by ionomycin was clearly large, implying a critical effect of the source of Ca²⁺ influx in PC boutons. Therefore, we suppose that the marked effect of ionomycin on release reflects higher elevation of bulk Ca²⁺ in the cytoplasm arising from non-site selective Ca²⁺-ionophore (Figure 8—figure supplement 1, p11, lines 327-334; lines 342-349).

In yet another scenario, recycled SVs in bafilomycin retain their fluorescence since they do not reacidify, but they come back to release sites to undergo new rounds of exocytosis. The new exocytosis events do not increase the fluorescence since the pH in the vicinity of synapto-pHluorin does not change. NH4Cl would then increase the fluorescence by revealing SVs that had not undergone exocytosis-endocytosis cycles during AP trains or KCl exposure. In this last scenario, the GPR55-sensitive SV pool would be a specific sub-pool of SVs that can be recycled by repetitive 400 AP trains.

We deeply appreciate the reviewer for pointing out this important possibility. We completely agree that this scenario can also explain the pool which is sensitive to GPR55. Therefore, we have added explanation of this possibility in the text (p15, lines 474–482).

Figure 6F shows calcium imaging measurements of PC varicosities. Unfortunately, crucial measurements are missing. It would have been revealing to compare calcium rises for the first and the last of the 8 400-AP trains. And to compare calcium rises elicited by 60 mM KCl before and after the series of 8 400-AP trains.

This is an important control experiment. Therefore, we have performed additional Ca²⁺ imaging during the eight 400-AP trains and KCl application. The new results shown in the present Figure 8—figure supplement 1 clearly suggest that Ca²⁺ rises are comparable between the first and eighth trains, and that additional Ca²⁺ influx (which was large in amplitude and wide in area) could still be evoked by KCl after the eight trains. The experiments are explained in the text p11, lines 327336.

Minor points:

(1) Introduction: The Introduction would benefit from a more substantial description of what is known about GPR55 and downstream signaling pathways. Right now, it is stated that GPR55 is 'potentially expressed in PCs': What are the arguments behind this statement? Also, the signaling pathway is discussed on p.12, much too late in the ms. Why not move this section to the Introduction?

We thank the reviewer for the helpful suggestion. As recommended, in the revised manuscript, we have changed the Introduction by moving the sentences from other sections, including speculation about the expression of GPR55 in Purkinje cells (Ryberg et al., 2007; Wu et al., 2013) (p3-4, lines 71-75) and downstream signaling pathways (Gα_q/PLC/IP₃/Ca²⁺ and Gα₁₃/RhoA/ROCK) (p3, 63-68).  

(2) Legend to Figures 1, 2, and 4: What is the EGTA concentration in these experiments?

As suggested, the EGTA concentrations (0.5 or 5 mM) used in the individual experiments have now been clearly indicated both in the figure legends and in the Methods section (p18, lines 585586).

(3) Fig. 3C: These experiments show that some SV pool is depleted by AM251. The authors state that this is the RRP, but other options are possible. In the calyx of Held, similar experiments are supposed to deplete not only the FRP (=RRP, presumably) but also the SRP.

We thank the reviewer for pointing out the important aspect related to category for vesicle pools. In PC boutons, the membrane capacitance increases in response to different duration of depolarization pulses in a manner fitted by a single exponential curve (see Figure 5C for example). Our previous study (Kawaguchi and Sakaba, 2015) noted that the vesicle pools corresponding to FRP and SRP may not be easy to distinguish in PCs, suggesting apparently single component. That’s the reason why we simply describe the component as RRP in the present manuscript. Still, as suggested, careful discussion about typical fast- and slow components would be helpful to interpret our present findings. Therefore in the revised manuscript, we have added a sentence to explain this issue (p7, lines 211-214).

(4) p. 8: When the 400 APs protocol is introduced, the corresponding frequency (20 Hz?) should be mentioned. This information comes only much later in the ms.

We are sorry for our insufficient explanation in the previous manuscript. As suggested, we have clearly written the stimulation frequency ‘20 Hz’ in the main text where the 400 APs protocol first appears (p9, lines 277-278).

(5) Figure 5, panels B and F: synapto-pHluorin is labelled twice 'synapto-pHluolin'.

Sorry for careless typos. Now, those are corrected (new Figure 7).

(6) Legend to Figure 5, last line: 'x' is missing in the last equation.

Thank you for the careful and kind check. Now, ‘x’ has been added to the last equation in the legend for new Figure 7.

(7) p. 7, Interpretation of EGTA effects: The authors frame their interpretation of EGTA effects around the distance between release sites and VGCCs. However since AM251 appears to alter the recruitment of SVs, a more parsimonious interpretation would be that EGTA modifies the calciumdependent movement of SVs towards release sites.

Thank you for suggesting an insightful scenario. We agree that the capacitance jump upon long depolarization pulse would include exocytosis of substantial amount of vesicles which are newly recruited during the Ca²⁺ increase. Then, as the reviewer states, EGTA possibly lowers the Ca²⁺dependent replenishment of synaptic vesicles, and this replenishment system might be the target of GPR55 activation. Therefore, we have now clearly added an explanation about this possibility in the text (p15, lines 474-482).

(8) p. 13, Interpretation of GPR55 sensitive SV pool: The authors suggest a larger distance to VGCCs for this pool compared to naïve SVs. An alternative could be that in the presence of GPR55, the recruitment to release sites would be less efficient.

This is also an insightful suggestion to speculate the causal relationship between the GPR55mediated reduction of vesicular release and the vesicle pools. Accordingly, we have revised the Discussion (see “Dynamics of synaptic vesicles among distinct functional pools”) by clearly telling about the possibility of decreased recruitment of vesicles to release sites after the GPR55 activation (p15, lines 474-482). By totally considering all the suggested scenario, we believe that the possible mechanisms for GPR55-mediated reduction of release are much more clearly explained in the revised manuscript.

Reviewer #3 (Recommendations for the authors):

(1) The time course of the agonist-induced suppression should be reported (Figure 1).

This is an important point to show data clearly, as suggested also by the reviewer 1. Accordingly, we have changed the figure panels to show time courses of agonist-induced suppression (shown in new Figures 1 and 4).  

(2) Show that the suppression of GABAergic transmission mediated by AM251 and LPI is eliminated in GPR55 KO mice.

We appreciate the reviewer for putting us to try this important experiment. Owing to the suggestion, we attempted to knock-down the GPR55 expression using CRISPR/Cas9 in cultured Purkinje cells. To avoid potential developmental compensations, here we adopted the CRISPR/Cas9-based genome editing approach, rather than using global knock out mice. Those GPR55-KO cells, as noted above in response to the comment #2 of reviewer #1, showed decreased fluorescent labeling of PC axon terminals to fluorescent-variant of AM251 (shown in new Figure 2) and abolishment of AM251-mediated suppression of vesicle exocytosis (Figure 3D and E). These results are explained in the text p5-6, lines 141-159; p6, lines 173-178.  

(3) Include references supporting AM251 and LPI as GPR55 agonists and specify the E50 concentrations for each agonist. Furthermore, provide details about the GPR55 antagonist CID16600046.

As suggested, we have added references regarding GPR55 agonists, AM251 and LPI. In the text, the following information was added: AM251, originally characterized as an inverse agonist for CB1, has also been reported to act as a GPR55 agonist (Ryberg et al., 2007; Henstridge et al., 2009) (p5, lines 115-116). LPI is an established endogenous GPR55 agonist (Oka et al., 2007; Henstridge et al., 2009) (p5, lines 127-129). The reported EC₅₀ values are ~ 30 nM for LPI (Oka et al., 2007, HEK cell assay) and 39 nM for AM251 (Ryberg et al., 2007, HEK cell assay) (p4, lines 94-95; p5, lines 127-129). Regarding the GPR55 antagonist CID16020046, detailed information (IC₅₀ = 0.21 µM for GPR55 without significant effect on CB1 receptor) was added in the text with an appropriate citation (Kargl et al., 2013) (p5, lines 123-127). These points have also been added to the Methods section (p17, lines 587-589).

(4) Regarding the onset delay (Figure 4C; page 8, lines 3-4), consider the following: "AM251 induced a modest yet significant synaptic delay, estimated by the time to the onset of release" (or something similar).

We thank the reviewer for suggesting helpful explanation. Accordingly, we have changed the sentence to explain the delayed onset (p9, lines 264-265).

These three points should be properly acknowledged in the Discussion:

(1) Are action potentials (APs)/depolarizations and ionomycin applications comparable? Ionomycin mediates a large calcium rise significantly slower than the calcium rise mediated by fast depolarization. Such presynaptic calcium dynamics could account, in part, for the different results.

The qualitative difference of Ca²⁺ increase between APs/depolarization-mediated ones and ionomycin-mediated one is an important point. Thank you for pointing out this issue. In the revised manuscript, we have added an explanation about the possible difference arising from the distinct dynamics of Ca²⁺ increases caused by direct depolarization of axon terminals or by ionomycin (p14, lines 452-453).

(2) Previous studies on hippocampal CA3-CA1 pyramidal cell synapses indicate that GPR55 activation enhances glutamate release through presynaptic calcium modulation while diminishing inhibitory postsynaptic strength by reducing GABAA receptors (Sylantyev et al., PNAS 2013; Rosenberg et al., Neuron 2023). In contrast, Inoshita and Kawaguchi discovered that GPR35 suppresses PC-DCN inhibitory transmission by decreasing GABA release without affecting inhibitory postsynaptic strength. Some potential explanation for this discrepancy is warranted.

We appreciate the reviewer for pointing out this important issue, and feel sorry for not providing an appropriate discussion about the possible interpretation in the previous manuscript. In the revised manuscript, we have added explanations for this discrepancy. First, PC terminals show only limited influence by elevated cytoplasmic Ca²⁺ through ER store on GABA release (Gomez et al., 2020) probably due to abundant calbindin. Second, our present data clearly show the GPR55 signals at PC terminals (although indirect, see Figure 2), while hippocampal inhibitory neuronal boutons somehow showed lower GPR55 levels compared with excitatory neuronal boutons (Rosenberg et al., Neuron, 2023). Third, the subtypes and/or anchoring mechanism for postsynaptic GABA_A receptors might be different between two distinct postsynaptic neurons in the hippocampus and the cerebellum. These factors are now clearly discussed in the text (p12, lines 380-396).

(3) Earlier work has suggested that CB1 receptor activation can alter the release machinery. Therefore, the observation that GPR55 activation induces changes in the RRP is not entirely surprising.

As pointed out, previous studies showed that CB1R influences the synaptic release machinery, rather than Ca²⁺ influx (Ramirez-Franco et al., 2014). In that context, as the reviewer says, the GPR55-mediated RRP change can be regarded as a similar synaptic modulation mechanism as the CB1-mediated one. However, considering the different downstream signaling pathways, G_12/13- or G_q-mediated one and G_i/o-mediated one, our findings would provide an important scope about the regulation mechanisms of release machinery, which should be further analyzed in the future study. Now we have added these points in discussion (p13-14, lines 435-439).

(4) Add a section about the limitations of this study (see Weaknesses above).

As suggested, we have added a section about the limitations of this study at present, which we could not address in the revision and should be addressed in the future (p15, lines 488-508). Particularly, the actual endogenous agonist to activate GPR55, and the physiological situation in which the agonist is produced, much more direct evidence for GPR55 presence at PC boutons, and the downstream mechanisms of GPR55-mediated suppression of GABA release are now clearly notified in that section.

(5) Double-check grammar and typos ("anandamid").

We are really sorry for the poor writings in the previous manuscript. Now, we have carefully checked the text.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The "number sense" refers to an imprecise and noisy representation of number. Many researchers propose that the number sense confers a fixed (exogenous) subjective representation of number that adheres to scalar variability, whereby the variance of the representation of number is linear in the number.

This manuscript investigates whether the representation of number is fixed, as usually assumed in the literature, or whether it is endogenous. The two dimensions on which the authors investigate this endogeneity are the subject's prior beliefs about stimuli values and the task objective. Using two experimental tasks, the authors collect data that are shown to violate scalar variability and are instead consistent with a model of optimal encoding and decoding, where the encoding phase depends endogenously on prior and task objectives. I believe the paper asks a critically important question. The literature in cognitive science, psychology, and increasingly in economics, has provided growing empirical evidence of decisionmaking consistent with efficient coding. However, the precise model mechanics can differ substantially across studies. This point was made forcefully in a paper by Ma and Woodford (2020, Behavioral & Brain Sciences), who argue that different researchers make different assumptions about the objective function and resource constraints across efficient coding models, leading to a proliferation of different models with ad-hoc assumptions. Thus, the possibility that optimal coding depends endogenously on the prior and the objective of the task, opens the door to a more parsimonious framework in which assumptions of the model can be constrained by environmental features. Along these lines, one of the authors' conclusions is that the degree of variability in subjective responses increases sublinearly in the width of the prior. And importantly, the degree of this sublinearity differs across the two tasks, in a manner that is consistent with a unified efficient coding model.

We thank Reviewer #1 for her/his comments and for placing our work in a broader context.

Comments:

(1) Modeling and implementation of estimation task

The biggest concern I have with the paper is about the experimental implementation and theoretical account of the estimation task. The salient features of the experimental data (Figure 1C) are that the standard deviations of subjects' estimated quantities are hump-shaped in the true stimulus x and that the standard deviation, conditional on the true stimulus x, is increasing in prior width. The authors attribute these features to a Bayesian encoding and decoding model in which the internal representation of the quantity is noisy, and the degree of noise depends on the prior - as in models of efficient coding (Wei and Stocker 2015 Nature Neuro; Bhui and Gershman 2018 Psych Review; Hahn and Wei 2024 Nature Neuro).

The concern I have is about the final "step" in the model, where the authors assume there is an additional layer of motor noise in selecting the response. The authors posit that the subject's selection of the response is drawn from a Gaussian with a mean set to the optimally decoded estimate x*(r), and variance set to a free parameter sigma_0^2. However, the authors also assume that the Gaussian distribution is "truncated to the prior range." This truncation is a nontrivial assumption, and I believe that on its own, it can explain many features of the data.

To see this, assume that there is no noise in the internal representation of x, there is only motor noise. This corresponds to a special case of the authors' model in which υ is set to 0. The model then reduces to a simple account in which responses are drawn from a Gaussian distribution centered at the true value of x, but with asymmetric noise due to the truncation. I simulated such a model with sigma_0=7. The resulting standard deviations of responses for each value of x (based on 1000 draws for each value of x), across the three different priors, reproduce the salient patterns of the standard deviation in Figure 1C: i) within each condition, the standard deviation is hump-shaped and peaks at x=60 and ii) conditional on x, standard deviation increases in prior width. The takeaway is that this simple model with only truncated motor noise - and without any noisy or efficient coding of internal representations - provides an alternative channel through which the prior affects behavior.

Of course, this does not imply that subjects' coding is not described by the efficient encoding and decoding model posited by the authors. However, it does suggest an important alternative mechanism for the authors' theoretical results in the estimation task. Moreover, some of the quantitative conclusions about the differences in behavior with the discrimination task would be greatly affected by the assumption of truncated motor noise.

Turning to the experiment, a basic question is whether such a truncation was actually implemented in the design. That is, was the range of the slider bar set to the range of the prior? (The methods section states that the size on the screen of the slider was proportional to the prior width, but it was unclear whether the bounds of the slider bar changed with the prior). If the slider bar range did depend on the prior, then it becomes difficult to interpret the data. If not, then perhaps one can perform analyses to understand how much the motor noise is responsible for the dependence of the standard deviation on both x and the prior width. Indeed, the authors emphasize that their model is best fit at α=0.48, which would seem to imply that the best fitting value of υ is strictly positive. However, it would be important to clarify whether the estimation procedure allowed for υ=0, or whether this noise parameter was constrained to be positive (i.e., clarify whether the estimation assumed noisy and efficient coding of internal representations).

We thank Reviewer #1 for her/his close attention to the motor-noise component of our model, in particular its truncation at the border of the prior. We agree that the truncated motor noise should be examined more closely as it affects the variance of responses. We address here the questions raised by the reviewer, and we detail the new analyses we have conducted.

First, regarding the experimental paradigm, we note that this truncation was indeed implemented in the design, i.e., the range of the slider bar corresponded to the range of the prior (we now indicate this more clearly in the manuscript). Subjects thus were not able to select an estimate that was not in the support of the prior, and it is precisely for this reason that we model the selection step with a truncated distribution, so that the model is consistent with the experimental setup. This truncation naturally decreases the response variability near the bounds, and this may affect differently the overall variability for the different priors, as noted by the reviewer in her/his simulations. We have conducted a series of analysis to investigate this question.

First, we consider a model in which there is no cognitive noise, but only motor noise. To answer one of the reviewer’s questions, the model-fitting procedure did allow for a vanishing cognitive noise (𝜈 = 0), i.e., it allowed for such a “motor-noise-only” mechanism to be the main account of the data. This value (𝜈 = 0), however, does not maximize the likelihood of the model, and thus this hypothesis is not the best account of the data. Nevertheless, we fit a model that enforces the absence of cognitive noise (i.e., with 𝜈 = 0). The BIC of this “motor-noise-only” model is higher than that of our best-fitting model by more than 1100, indicating very strong support for the best-fitting model, which features a positive cognitive noise (𝜈 > 0), and 𝛼 = 1/2, as in our theoretical proposal.

Furthermore, the standard deviation of responses predicted by the motor-noise-only model overestimates substantially the variability of subjects' responses in the Narrow and Medium conditions (Figure 4, panel b), while the predictions of the best-fitting model are much closer to the behavioral data (panel a). Finally, the variances predicted by this model do not increase linearly with the prior width (contrary to the behavioral data). Instead, the variance increases more between the Narrow and the Medium priors than between the Medium and the Wide priors, as the effects of the bounds attenuate with the wider prior (panel c, solid green line).

To further this analysis we fit in addition a model with no cognitive noise (𝜈 = 0), but in which we now allow the degree of motor noise, 𝜎₀, to depend on the prior. Our reasoning is that if the truncated motor noise were the sole explanation for the increase in subjects' variance with the prior width, then we would expect the noise levels for the three priors to be roughly equal. We find instead that they are different (with values of 5.9, 8.3, and 9.8, for the prior widths 20, 40, and 60, respectively, when pooling subjects; and when fitting subjects individually the distributions of parameter values exhibit a clear increase; see panels c and d above). This model moreover yields a BIC higher by more than 590 than our best-fitting model. We note in addition that these parameter values differ in such a way that they result in response variances that are a linear function of the prior width, as found in the behavioral data, although they overestimate the subjects' variances (panel c, dotted green line). This linear increase is directly predicted by our best-fitting model, which has one less parameter (2 vs. 3), and which moreover accurately predicts the variability of subjects across priors (panel c, pink line). Hence the data do not support a model with no cognitive noise and with only a constant, truncated motor noise.

We also consider another possibility, that in addition to truncated motor noise there is in fact a degree of cognitive noise, but one that is insensitive to the width of the prior. In other words, there is cognitive imprecision, but it does not efficiently adapt to the prior range, as in our proposal. This corresponds to setting 𝛼 = 0, in our model; but this specification of the model results in a poor fit, with a BIC higher by more than 300 than that of the best-fitting model, whose cognitive noise scales with the exponent 𝛼 = 1/2, consistent with our theory. Thus our data do not support the hypothesis of a cognitive noise that does not scale with the prior range; instead, subjects' responses support a model in which the variance of the cognitive noise increases linearly with the prior range.

We note in addition that there is inter-subject variability: different subjects have different degrees of imprecision. But if the source of the imprecision was the truncated motor noise, then different degrees of truncated noise should result in different relationships between the behavioral variance and the prior widths: subjects with smaller noise should be relatively insensitive to the width of the prior, while subjects with greater noise should be more sensitive. In that case, when fitting the subjects with the model in which the imprecision scales as a power of the width, we should expect subjects to exhibit a diversity of best-fitting parameter values 𝛼. Instead, as noted, we find that the data is best captured by a single exponent 𝛼 = 1/2, equal for all the subjects. This suggests that although the “baseline level” of the imprecision may differ per subject, the way that their imprecision increases as a function of the prior width is the same for all the subjects, a behavior that is not explained by truncated noise alone.

Furthermore, Prat-Carrabin, Harl, and Gershman 2025 present behavioral results obtained in a similar numerosity-estimation task, with the same prior ranges, but with the experimental difference that the slider was not limited to the range of the current prior: instead it had the same width in all three conditions, and covered in all trials a range wider than that of the Wide prior (from 25 to 95). The behavioral variance observed in this study increases linearly with the prior range, as in our results. Thus we conclude that the linear increase in subjects' variability does not originate in the bounds of the experimental slider.

Finally, Prat-Carrabin et al. 2025 presents an fMRI study involving a similar numerosityestimation experiment. This study shows that numerosity-sensitive neural populations in human parietal cortex adapt their tuning properties to the current numerical range, resulting in less precise neural encoding when the range is wider. This substantiates the notion that the degree of imprecision in cognitive noise adapts to the prior range, as in our proposal.

Overall, we conclude that the linear increase of behavioral variability that we document originates in the endogenous adaptation, across conditions, of the amount of imprecision in the internal encoding of numerosities.

We now include these analyses in a new section of the Methods (p. 24-27), which we summarize in the main text (p. 7-8). The Figure above is now included (as Figure 4). We also now cite the references mentioned by Reviewer #1 and which we had not already cited (Bhui and Gershman 2018 Psych Review; Hahn and Wei 2024 Nature Neuro).

References:

Prat-Carrabin, A., Harl, M. V., & Gershman, S. J. (2025). Fast efficient coding and sensory adaptation in gain-adaptive recurrent networks (p. 2025.07.11.664261). bioRxiv. https://doi.org/10.1101/2025.07.11.664261

Prat-Carrabin, A., de Hollander, G., Bedi, S., Gershman, S. J., & Ruff, C. C. (2025). Distributed range adaptation in human parietal encoding of numbers (p. 2025.09.25.675916). bioRxiv. https://doi.org/10.1101/2025.09.25.675916

(2) Differences across tasks

A main takeaway from the paper is that optimal coding depends on the expected reward function in each task. This is the explanation for why the degree of sublinearity between standard deviation and prior width changes across the estimation and discrimination task. But besides the two different reward functions, there are also other differences across the two tasks. For example, the estimation task involves a single array of dots, whereas the discrimination task involves a pair of sequences of Arabic numerals. Related to the discussion above, in the estimation task the response scale is continuous whereas in the discrimination task, responses are binary. Is it possible that these other differences in the task could contribute to the observed different degrees of sublinearity? It is likely beyond the scope of the paper to incorporate these differences into the model, but such differences across the two tasks should be discussed as potential drivers of differences in observed behavior.

If it becomes too difficult to interpret the data from the estimation task due to the slider bar varying with the prior range, then which of the paper's conclusions would still follow when restricting the analysis to the discrimination task?

There are indeed several differences between the estimation and discrimination tasks that could, in principle, contribute to the quantitative differences observed between them. The fact that the estimation task requires a continuous numerical report whereas the discrimination task involves a binary choice is captured in our model by incorporating distinct loss functions for the two tasks (Eq. 4). This distinction is a key element of the theoretical framework, as it determines the optimal allocation of representational precision. We agree with Reviewer #1 that another important difference is that the estimation task involves non-symbolic dot arrays while the discrimination task uses short sequences of Arabic numerals, which could also affect performance through distinct perceptual or cognitive processes. Although we cannot exclude this possibility, it is unclear why such a difference in stimulus format would produce the specific quantitative patterns that we observe — and that are predicted by our proposal, namely, the sublinear scalings with task-dependent exponents. Each experiment, taken independently, supports the model's central prediction that the precision of internal representations scales sublinearly with the width of the prior distribution. Taken together, the two tasks show that this dependence itself varies with the observer's objective, confirming that perceptual precision is endogenously determined by both the statistical context and the task goal.

We agree with Reviewer #1 that this point should be mentioned; we now do so in the Discussion (p. 17-18).

(3) Placement literature

One closely related experiment to the discrimination task in the current paper can be found in Frydman and Jin (2022 Quarterly Journal of Economics). Those authors also experimentally vary the width of a uniform prior in a discrimination task using Arabic numerals, in order to test principles of efficient coding. Consistent with the current findings, Frydman and Jin find that subjects exhibit greater precision when making judgments about numbers drawn from a narrower distribution. However, what the current manuscript does is it goes beyond Frydman and Jin by modeling and experimentally varying task objectives to understand and test the effects on optimal coding. This contribution should be highlighted and contrasted against the earlier experimental work of Frydman and Jin to better articulate the novelty of the current manuscript.

We thank Reviewer #1 and we agree that the work of Frydman and Jin is highly relevant to our study. Instead of comparing our contributions to theirs, we have decided to have a close look at their data, in light of our theoretical proposal. This enables us to test the predictions of our theory against human choices made in a rather different decision situation than that of our discrimination task.

Thus we looked, in their data, at the participants' probability of choosing the risky lottery instead of the certain amount, as a function of the difference between the lottery's expected value (pX) and the certain amount (C; we also added a small bias term to the certain option; such bias was not necessary with our discrimination data, presumably because of the inherent symmetry of our task).

We find, as did Frydman and Jin, and similarly to our discrimination task, that the participants are more precise when the proposed amounts are sampled from a Narrow prior, in comparison to a Wide prior (see figure above, first panel). But we also find, as in our discrimination task, that when normalizing the value difference by the prior width participants are more sensitive to this normalized difference in the Wide condition than in the Narrow one, suggesting that their imprecision scales across conditions by a smaller factor than the prior width (last panel). And we find, consistent with our discrimination data and with our theory, that choice probabilities in the two conditions match very well when normalizing the difference by the prior width raised to the exponent 3/4 (third panel).

Model fitting supports this observation. We fit the data to our model (described by Eq. 3), with the addition of a lapse probability and of a bias, and with different values of the exponent 𝛼. The best-fitting model is the one with 𝛼 = 3/4. Its BIC (35,419) is lower than those of the models with 𝛼 = 1, ½, and 0 (by 142, 39, and 514, respectively). It is also lower by 2.14 than a model in which 𝛼 is left as a free parameter (in which case the bestfitting 𝛼 is 0.68, a value not far from 3/4). We emphasize that these BIC values indicate that the hypotheses 𝛼 = 0 and 𝛼 =1 are clearly rejected, i.e., the participants' imprecision increases with the prior width (𝛼 > 0), but sublinearly (𝛼 < 1). In other words, the responses collected by Frydman and Jin in a risky-choice task are quantitatively consistent with our results obtained in a number-discrimination task, and they further substantiate our model of endogenous precision.

We moreover note that their proposed model is similar to ours, in that the decision-maker is allowed to optimize a noisy encoding scheme to the prior, subject to a ‘capacity constraint’ on the number 𝑛 of encoding signals that can be obtained. Crucially, this capacity constraint is assumed to be a property of the decision-maker that does not change across priors, and thus 𝑛 is fixed across prior widths. Therefore, their model predicts that the participants' imprecision should scale linearly with the prior width (this is also what we obtain in our model if we don’t optimize a similar parameter; see the revised presentation of the model on p. 12-13). We note that when they fit this parameter, 𝑛, separately across conditions, they find that it is larger with the wider prior. This is precisely what our model of endogenous precision predicts. In turn this predicts a sublinear scaling of the imprecision, instead of the linear one that would result from a fixed 𝑛, and indeed we find a sublinear scaling in both their dataset and ours. What is more, in both datasets the sublinear scaling is best captured by the exponent 𝛼 = 3/4, as we predict.

This analysis of another independent dataset obtained with a different experimental paradigm significantly strengthens our conclusions. Thus we added to the Results section a new subsection discussing this analysis, and the figure above now appears as Figure 3. We also mention it in the Introduction (l. 87-89) and in the Discussion (l. 556-557).

Reviewer #2 (Public review):

Summary:

This paper provides an ingenious experimental test of an efficient coding objective based on optimization as a task success. The key idea is that different tasks (estimation vs discrimination) will, under the proposed model, lead to a different scaling between the encoding precision and the width of the prior distribution. Empirical evidence in two tasks involving number perception supports this idea.

Strengths:

The paper provides an elegant test of a prediction made by a certain class of efficient coding models previously investigated theoretically by the authors.

The results in experiments and modeling suggest that competing efficient coding models, optimizing mutual information alone, may be incomplete by missing the role of the task.

We thank Reviewer #2 for her/his positive comments on our work.

Weaknesses:

The claims would be more strongly validated if data were present at more than two widths in the discrimination experiment.

We agree that including additional prior widths would allow for a more detailed validation of the predicted scaling law, in particular in the discrimination task. Our design choices across the two experiments reflect a trade-off between the number of prior widths and the number of trials per condition. In the estimation task, we include three widths because this is necessary to identify all three parameters of the model: the variance of the motor noise , the baseline variance of internal imprecision (𝜈²), and the scaling exponent (𝛼). Extending both tasks to include additional prior widths would indeed provide a more robust test of the predicted scaling law. We now note this point in the revised Discussion (p. 17).

A very strong prediction of the model -- which determines encoding entirely from prior and task -- is that Fisher Information is uniform throughout the range, strongly at odds with the traditional assumption of imprecision increasing with the numerosity (Weber/Fechner law). This prediction should be checked against the data collected. It may not be trivial to determine this in the Estimation experiment, but should be feasible in the Discrimination experiment in the Wide condition: Is there really no difference in discriminability at numbers close to 10 vs numbers close to 90? Figure 2 collapses over those, so it's not evident whether such a difference holds or not. I'd have loved to look into this in reviewing, but the authors have not yet made their data publicly available - I strongly encourage them to do so.

Importantly, the inverse u-shaped pattern in Figure 1 is itself compatible with a Weber's-law-based encoding, as shown by simulation in Figure 5d in Hahn&Wei [1]. This suggests a potential competing variant account, in apparent qualitative agreement with the findings reported: the encoding is compatible with Fisher's law, and only a single scalar, the magnitude of sensory noise, is optimized for the task for the loss function (3). As this account would be substantially more in line with traditional accounts of numerosity perception - while still exhibiting taskdependence of encoding as proposed by the authors - it would be worth investigating if it can be ruled out based on the data gathered for this paper.

References:

[1] Hahn & Wei, A unifying theory explains seemingly contradictory biases in perceptual estimation, Nature Neuroscience 2024

Indeed our efficient-coding model predicts that a uniform should result in a constant Fisher-information function, and we agree with Reviewer #2 that this is at odds with the common assumption that the imprecision increases with the magnitude. To investigate this possibility, we now consider, in the revised manuscript, a more general model of Gaussian encoding, in which the internal representation, 𝑟, is normally distributed around an increasing transformation of the number, 𝜇(𝑥), as

𝑟|𝑥~𝑁(𝜇(𝑥), 𝜈²𝑤^{2 𝛼}),

where the encoding function, 𝜇(𝑥), can be either linear (𝜇(𝑥) = 𝑥) or logarithmic (𝜇(𝑥) = log (𝑥)). This allows us to test whether the data are better captured by a uniform Fisher information (as predicted by the linear encoding under a uniform prior) or by a compressed, Weber-like representation.

We note, first, that in both tasks our conclusions regarding the dependence of the imprecision on the prior width remain unchanged, whether we choose the linear encoding or the logarithmic encoding. With both choice of encoding, the estimation task is best fit by a model with 𝛼 = 1/2, and the discrimination task by a model with 𝛼 = 3/4, implying a sublinear scaling of the variance with the width of the prior, in quantitative agreement with our theory.

In the estimation task, the logarithmic encoding yields a significantly lower BIC than the linear one, by more than 380 (see Table 1). The results are less clear in the discrimination task, where the BIC with the logarithmic encoding is lower by 2.1 when pooling together the responses of all the subject, but it is larger by 2.6 when fitting each subject individually. We conduct in addition a “Bayesian model selection” procedure, to estimate the relative prevalence of each encoding among subjects. The resulting estimate of the fraction of the population that is best fit by the logarithmic encoding is 87.6% in the estimation task, and 45.9% in the discrimination task (vs. 12.4% and 54.1% for the linear encoding).

To further investigate the behavior of subject in the Discrimination task, we look at their proportion of correct choices in the Wide and Narrow conditions, for the trials in which both averages are below the middle value of the prior, and for those in which both are above the middle value. We find no significant difference in the Narrow condition (see Figure below). In the Wide condition, the proportion of correct responses appear larger when the averages are small (with a significant difference when binning together the trials in which the absolute difference between the averages is between 4 and 12; Fisher's exact test p-value: 0.030).

To complement this analysis, we fit a probit model with lapses, which is equivalent to our Gaussian model with linear encoding, but allowing the noise scale parameter to differ when both averages are above, or below, the middle value of the prior. We fit this model separately in each condition, only on the trials in which both averages are either above or below the middle value; and we test a more constrained model in which the scale parameter is equal for both small and large averages. In the Narrow condition, a likelihood-ratio test does not reject the null hypothesis that the scale parameter is constant (𝜒²(1) = 0.026, 𝑝 = 0.87), but in the Wide condition this hypothesis is rejected (𝜒² (1) = 7.6, 𝑝 = 0.006). In this condition the best-fitting scale parameter is 29% larger (9.4 vs. 6.3) with the large averages than with the small averages, pointing to a larger imprecision with the larger numbers.

These results and the prevalence of the Weber/Fechner encoding prompt us to consider, in our efficient-coding model, the hypothesis that a logarithmic compression is an additional constraint on the possible encoding schemes. In our model, the internal representation (𝑟) could take any form as long as its Fisher information verified the constraint in Eq. 5 on the integral of its square-root. We now consider a strong, additional constraint: that over the support of the prior, the Fisher information of the signal must be of the form that one would obtain with a logarithmic encoding, i.e., 𝐼(𝑥) ∝ 1/𝑥². (For the sake of generality we choose this specification instead of directly assuming a logarithmic encoding, because other types of encoding schemes yield a Fisher information of this form, e.g., one with “multiplicative noise” (Zhou et al., 2024); we do not seek, here, to distinguish between these different possibilities). We solve the same efficient-coding optimization problem (Eq. 6), but now with this additional constraint. We find that the resulting optimal Fisher information is approximately:

, for the estimation task,

and , for the discrimination task,

for any 𝑥 on the support of the prior, and where 𝑥_mid is the middle of the prior and 𝜃 is a constant. These Fisher-information functions differ from the one previously obtained without the additional constraint (Eq. 9), in that they fall off as 1/𝑥², consistent with our additional constraint. However, we note that the dependence on the prior width, 𝑤, is identical: here also, the imprecision is proportional to , in the estimation task, and to 𝑤^3/4, in the discrimination task.

In its logarithmic variant (𝜇(𝑥) = log (𝑥)), the Fisher information of the model of Gaussian representations that we have considered throughout is 1/(𝑥 𝜈 𝑤^𝛼)². It is thus consistent with the predictions just presented, if 𝛼 = 1/2 for the estimation task, and 𝛼 = 3/4 for the discrimination task, i.e., the two values that best fit the data.

This is precisely the model suggested by Reviewer #2. Overall, we conclude that with both linear and logarithmic encoding schemes, our efficient-coding model — wherein the degree of imprecision is endogenously determined — accounts for the task-dependent sublinear scaling of the imprecision that we observe in behavioral data. As for the imprecision across numbers, a sizable fraction of subjects, particularly in the estimation task, are best fit by the logarithmic encoding, consistent with previous reports that numbers are often represented on a compressed, approximately logarithmic scale. This encoding may itself reflect an efficient adaptation to a long-term environmental prior that is skewed, with smaller numbers occurring more frequently, leading to greater representational precision. This pattern is less clear in the discrimination task. It is possible that the rate at which the precision decreases across numbers itself depends on the task, such that not only the overall level of imprecision, but also its variation across numbers, may be modulated by the task's demands. In this study we have focused on the endogenous choice of the overall precision, but an avenue for future research would be to examine how this adaptation interacts with the detailed shape of the encoding across numbers.

In the revised manuscript, we have modified the presentation of the model to include the transformation 𝜇(𝑥) (p. 6-7 and 10-11). We have updated accordingly Table 1 (shown above; p. 24), which reports the BICs of all the models for the estimation task (and which now includes the models with logarithmic encoding). There is now a section in the Results dedicated to the question of the logarithmic compression, which includes the efficientcoding model constrained by the logarithmic encoding (p. 15-16). The results on the performance of subjects with larger numbers are presented in Methods (p. 29-31), and mentioned in the main text (p. 14-15). The Methods also provides details about the efficient-coding model with logarithmic encoding (p. 32-33). These results are further commented on in the Discussion (p. 18). Finally, the data and code are now available online at this address: https://osf.io/d6k3m/ , which we note on p. 33.

Reference

Zhou, J., Duong, L. R., & Simoncelli, E. P. (2024). A unified framework for perceived magnitude and discriminability of sensory stimuli. Proceedings of the National Academy of Sciences, 121(25), e2312293121. https://doi.org/10.1073/pnas.2312293121

Reviewer #3 (Public review):

Summary:

This work demonstrates that people's imprecision in numeric perception varies with the stimulus context and task goal. By measuring imprecision across different widths of uniform prior distributions in estimation and discrimination tasks, the authors find that imprecision changes sublinearly with prior width, challenging previous range normalization models. They further show that these changes align with the efficient encoding model, where decision-makers balance expected rewards and encoding costs optimally.

Strengths:

The experimental design is straightforward, controlling the mean of the number distribution while varying the prior width. By assessing estimation errors and discrimination accuracy, the authors effectively highlight how imprecision adjusts across conditions.

The model's predictions align well with the data, with the exponential terms (1/2 and 3/4) of imprecision changes matching the empirical results impressively.

We thank Reviewer #3 for his/her positive comments on our work.

Weaknesses:

Some details in the model section are unclear. Specifically, I'm puzzled by the Wiener process assumption where r∣x∼N(m(x)T,s^2T). Does this imply that both the representation of number x and the noise are nearly zero at the beginning, increasing as observation time progresses? This seems counterintuitive, and a clearer explanation would be helpful.

In the original formulation of the model, indeed both the mean of the representation and its variance are nearly zero when T is also near zero, but in such a way that the Fisher information, 𝑇(𝑚′(𝑥)/𝑠)², is proportional to 𝑇. We note that a different specification, with a mean 𝑚(𝑥) (instead of 𝑚(𝑥)𝑇) and a variance 𝑠²/𝑇 (instead of 𝑠²𝑇), i.e., 𝑟|𝑥~𝑁(𝑚(𝑥), 𝑠²/𝑇), for 𝑇 > 0, would result in the same Fisher information.

In any event, in the revised manuscript, we now formulate the model differently. Specifically, we assume that the encoding results from an accumulation of independent, identically-distributed signals, but the precision of each signal is limited, and each of them entails a cost. Formally, we posit, first, that the Fisher information of one signal, 𝐼₁(𝑥), is subject to the constraint:

This constraint appears in many other efficient-coding models in the literature (Wei & Stocker 2015, 2016; Wang et al. 2016; Morais & Pillow, 2018; etc.), and it arises naturally for unidimensional encoding channels (Prat-Carrabin & Woodford, 2001; e.g., for a neuron with a sigmoidal tuning curve, it is equivalent to assuming that the range of possible firing rates is bounded). Second, we assume that the observer incurs a cost each time a signal is emitted (e.g., the energy resources consumed by action potentials). The total cost is thus proportional to the number of signals, which we denote by 𝑛. More signals, however, allow for a better precision: specifically, under the assumption of independent signals, the total Fisher information resulting from 𝑛 signals is the sum of the Fisher information of each signal, i.e., 𝐼(𝑥) = 𝑛𝐼₁(𝑥).

A tradeoff ensues between the increased precision brought by accumulating more signals, and the cost of these signals. We assume that the observer chooses the function 𝐼₁(.) and the number 𝑛 of signals that solve the minimization problem subject to ,

where 𝜆 > 0. We can first solve this problem for the Fisher information of one signal, 𝐼₁(𝑥). In the case of a uniform prior of width 𝑤, we find that it is zero outside of the support of the prior, and

for any 𝑥 on the support of the prior. This intermediate result corresponds to the optimal Fisher information of an observer who is not allowed to choose the number of signal, 𝑛, (and who receives instead 𝑛 = 1 signal). It is the solution predicted by the efficient-coding models mentioned above, that include the constraint on 𝐼₁(𝑥), but that do not allow for the observer to choose the amount of signals, 𝑛. With this solution, the scale of the observer's imprecision, , is proportional to 𝑤, and it does not depend on the task — contrary to our experimental results.

Solving the optimization problem for 𝑛, in addition to 𝐼₁(𝑥), we find that with a uniform prior the optimal number is proportional to 𝑤 in the estimation task, and to in the discrimination task (specifically, treating 𝑛 as continuous, we obtain ). In other words, the observer chooses to obtain more signals when the prior is wider, and in a way that depends on the task. We give the general solution for the total Fisher information, 𝐼(𝑥) = 𝑛𝐼₁(𝑥), in the case of a prior 𝜋(𝑥) that is not necessarily uniform:

where 𝜃 = 𝜆/𝐾. This is of course the same solution that we obtained in the original manuscript.

We hope that this new formulation of the efficient-coding model will seem more intuitive to the reader (p. 12-13 in the revised manuscript).

The authors explore range normalization models with Gaussian representation, but another common approach is the logarithmic representation (Barretto-García et al., 2023; Khaw et al., 2021). Could the logarithmic representation similarly lead to sublinearity in noise and distribution width?

We agree with Reviewer #3 that a common approach when modeling the perception of numbers is to consider a logarithmic encoding. We have conducted several analyzes that examine this proposal. These are presented in detail in our response to a comment of Reviewer #2, above (p. 11-14 of this document). We summarize shortly our findings, here:

(i) A model with a logarithmic encoding better fits a majority of subjects in the estimation task, but a bit less than half the subjects in the discrimination task.

(ii) The examination of the performance of subjects in the discrimination task, however, suggests that in the Wide condition they discriminate slightly better the small numbers, as compared to the larger numbers.

(iii) We consider a constrained version of our efficient-coding model, in which the Fisher information must be consistent with that of a logarithmic encoding (i.e., decreasing as 1/𝑥²); we find that the resulting optimal Fisher information depends on the prior width in the same way than without the constraint, i.e., a scaling of the imprecision with , in the estimation task, and with 𝑤^3/4, in the discrimination task.

(iv) When considering the model with logarithmic encoding, we find that it best fits the data when its imprecision scales with the width with the same exponents, i.e., , in the estimation task (𝛼 = 1/2), and 𝑤^3/4, in the discrimination task (𝛼 = 3/4). In other words, the data support the predictions of our theoretical model.

In the revised manuscript, we have modified accordingly the presentation of the model (p. 6-7 and 10-11), the Tables 1 (p. 24) and 2 (p. 30) which report the BICs. There is now a section in the Results dedicated to the question of the logarithmic compression, including the efficient-coding model constrained by the logarithmic encoding (p. 15-16). The results on the performance of subjects with larger numbers are presented in Methods (p. 29-31), and mentioned in the main text (p. 15-16). The Methods also provides details about the efficient-coding model with logarithmic encoding (p. 32-33). These results are further commented on in the Discussion (p. 18). Finally, we now cite the articles mentioned by Reviewer #3 (Barretto-García et al., 2023; Khaw et al., 2021).

Additionally, Heng et al. (2020) found that subjects did not alter their encoding strategy across different task goals, which seems inconsistent with the fully adaptive representation proposed here. I didn't find the analysis of participants' temporal dynamics of adaptation. The behavioral results in the manuscript seem to imply that the subjects adopted different coding schemes in a very short period of time. Yet in previous studies of adaptation, experimental results seem to be more supportive of a partial adaptive behavior (Bujold et al., 2021; Heng et al., 2020), which might balance experimental and real-world prior distributions. Analyzing temporal dynamics might provide more insight. Noting that the authors informed subjects about the shape of the prior distribution before the experiment, do the results in this manuscript suggest a top-down rapid modulation of number representation?

We thank Reviewer #3 for his/her comment and for pointing to these articles. The Reviewer raises several points — that of the dynamics of adaptation, that of the adaptation to the prior, and that of the adaptation to the task. We address each of them.

To investigate the dynamics of the subjects’ adaptation, we examined separately, in each task, the responses obtained in the trials in the first and second halves of each condition. In the estimation task, the standard deviations of responses, as a function of the presented number and of the prior width, are very similar in the two halves (see Figure 8, panel a). The Bonferroni-Holm-corrected p-values of Levene's tests of equality of the variances across the two halves are all above 0.13, and thus we do not reject the hypothesis that the variance in the first half of the trials is equal to the variance in the second half. Moreover, the variance in both halves appear to be a linear function of the width, rather than the squared width (panel b). We conclude that the behavior of subjects in the estimation task is stable across each experimental condition, including the sublinear scaling of their imprecision.

In the discrimination task, the subjects' choice probabilities, as a function of the difference between the averages of the red and blue numbers, are similar in the first and second halves of trials (panel c). The Bonferroni-Holm-corrected p-values of Fisher exact tests of equality of proportions (in bins of the average difference that contain about 500 trials each) are all above 0.9, and thus we do not reject the hypothesis that the choice probabilities are equal, in the first and second halves of the trials. Furthermore, the choice probabilities as a function of the absolute average difference normalized by the prior width raised to the exponent 3/4 are all similar, across session halves and across prior widths, suggesting that the sublinear scaling that we find is a stable behavior of subjects (panel d).

Overall, we conclude that the behavior we exhibit in both tasks is stable over the course of each experimental condition. We note that in both experiments, subjects were explicitly informed of the prior distribution at the beginning of each condition, and each condition included two preliminary training phases that familiarized them with the prior (the specifics for each task are detailed in the Methods section).

As pointed out by Reviewer #3, Heng et al. (2020) and Bujold et al. (2021) report a partial adaptation of encoding to recently experienced distributions. We note that in our study, a sizable fraction of subjects, particularly in the estimation task, are best fit by the logarithmic encoding. This suggests that, while subjects adapt to the experimental prior, they retain a residual logarithmic compression — an encoding that itself would be efficient under a long-term, skewed prior in which smaller numbers are more frequent. In that sense our findings are thus consistent with the partial adaptation of Heng et al. (2020) and Bujold et al. (2021). At the same time, the same sublinear scaling of imprecision that we find in our study has been obtained in a numerosity-estimation task in which the prior was changed on every trial (Prat-Carrabin et al., 2025), indicating that the adaptation to the prior can occur quickly (on the order of a second) — possibly through a fast top-down modulation of the encoding, as suggested by Reviewer #3. These findings suggest that on a short timescale the encoding adapts efficiently to the prior (as evidenced by the scaling in imprecision), but within structural constraints (the logarithmic encoding).

Regarding the adaptation to the task, Heng et al. (2020) indeed do not find subjects to be adapting their encoding, across two discrimination tasks (one in which the subject is rewarded for making the correct choice, and one in which the subject is rewarded with the chosen option). A difference with our paradigm is that their task involves simultaneous presentation of two dot arrays, while our discrimination task uses two interleaved sequences of Arabic numerals. More importantly, we do not directly compare the encoding between the estimation and discrimination tasks. Instead, we show that within each task, the adaptation to the prior is quantitatively consistent with the optimal coding predicted for that task's objective, as reflected in the task-specific sublinear scaling exponents. Directly contrasting the encoding across tasks would be a very interesting direction for future work.

In the revised manuscript, we present the analysis on the stability of subjects’ behavior in the Methods section (p. 29), and we mention it in the main text when presenting the results of the estimation task (p. 5) and of the discrimination task (p. 8-10). In the Discussion, we cite Heng et al. (2020) and Bujold et al. (2021) and comment on the adaptation to the prior and to the task (p. 18).

Barretto-García, M., De Hollander, G., Grueschow, M., Polanía, R., Woodford, M., & Ruff, C. C. (2023). Individual risk attitudes arise from noise in neurocognitive magnitude representations. Nature Human Behaviour, 7(9), 15511567. https://doi.org/10.1038/s41562-023-01643-4

Bujold, P. M., Ferrari-Toniolo, S., & Schultz, W. (2021). Adaptation of utility functions to reward distribution in rhesus monkeys. Cognition, 214, 104764. https://doi.org/10.1016/j.cognition.2021.104764

Heng, J. A., Woodford, M., & Polania, R. (2020). Efficient sampling and noisy decisions. eLife, 9, e54962. https://doi.org/10.7554/eLife.54962

Khaw, M. W., Li, Z., & Woodford, M. (2021). Cognitive Imprecision and SmallStakes Risk Aversion. The Review of Economic Studies, 88(4), 19792013. https://doi.org/10.1093/restud/rdaa044

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(1) As mentioned above, the result of inverse u-shaped variability is in strong qualitative agreement with the predictions of a generic Bayesian encoding-decoding model of a flat prior, even under a standard encoding respecting Weber's law, as shown in Figure 5d in: Hahn & Wei, A unifying theory explains seemingly contradictory biases in perceptual estimation, Nature Neuroscience 2024. This paper should probably be cited.

We now cite Hahn & Wei, 2024. We comment above on our analyzes regarding the logarithmic encoding.

(2) "Requests for the data can be sent via email to the corresponding author" Why are the data not made openly available? Barring ethical or legal concerns (which are not apparent for this type of data), there is no reason not to make data and code open.

"Requests for the code used for all analyses can be sent via email to the corresponding author." Same: why not make them open?

We agree that it is good practice to make the data and code publicly available. They are now available here: https://osf.io/d6k3m/

Reviewer #3 (Recommendations for the authors):

The orange dot in Figure 1C does not appear to be described in the figure caption, although an explanation of it is mentioned in the main text.

We thank Reviewer #3 for pointing out this omission. We now include explanations in the caption.

I hope the authors will consider making their data publicly available on OSF or another platform.

The data and code are now publicly available on OSF: https://osf.io/d6k3m/

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors aimed to assess the variability in the expression of surface protein multigene families between amastigote and trypomastigote Trypanosoma cruzi, as well as between individuals within each population. The analysis presented shows higher expression of multigene family transcripts in trypomastigotes compared to amastigotes and that there is variation in which copies are expressed between individual parasites. Notably, they find no clear subpopulations expressing previously characterised trans-sialidase groups. The mapping accuracy to these multicopy genes requires demonstration to confirm this, and the analysis could be extended further to probe the features of the top expressed genes and the other multigene families also identified as variable.

Strengths:

The authors successfully process methanol-fixed parasites with the 10x Genomics platform. This approach is valuable for other studies where using live parasites for these methods is logistically challenging.

Weaknesses:

The authors describe a single experiment, which lacks controls or complementation with other approaches and the investigation is limited to the trans-sialidase transcripts.

It would be more convincing to show either bioinformatically or by carrying out a controlled experiment, that the sequencing generated has been mapped accurately to different members of multigene families to distinguish their expression. If mapping to the multigene families is inaccurate, this will impact the transcript counts and downstream analysis.

We thank the reviewer for raising these important points.

We agree that the analysis of multigene families at the single-cell level is an important question, particularly given the heterogeneity observed across several of them. However, the aim of this short report is not to provide a comprehensive analysis of the entire experiment, but rather to focus on what we consider an important biological phenomenon observed in TcTS genes.

Regarding the mapping accuracy of the reads, we acknowledge that this can limit the disambiguation of highly similar multicopy transcripts. This is, in fact, a common challenge when analyzing transcriptomic data from T. cruzi.

To address this issue, we analyzed the sequence identity of the 3′ ends of TcS transcripts (defined as the 3′UTR plus 20% of the CDS region). As shown in Author response image 1, these regions display a median sequence identity of approximately 25%, indicating that sufficient sequence divergence exists for mapping algorithms to use during read assignment.

In addition, it is important to note that kallisto, the software used in our analysis, was specifically designed to address multimapping reads through pseudoalignment combined with an expectation-maximization algorithm that probabilistically assigns reads across compatible transcripts.

To directly assess performance, we simulated reads from the T. cruzi transcriptome used in this study (3′UTRs plus 20% of the CDS regions) and compared two mapping/counting strategies: (a) transcriptome pseudoalignment using kallisto, and (b) genome alignment followed by counting using STAR + featureCounts. The latter approximates the strategy implemented in CellRanger, the standard pipeline for quantifying expression levels from 10X Genomics single cell RNA-seq data. We found that kallisto recovered the simulated “true” counts with substantially higher accuracy than STAR + featureCounts (Pearson correlation: all genes, 0.991 vs 0.595; surface protein genes, 0.9996 vs 0.827; trans-sialidase (TcS) genes, 0.9998 vs 0.773). These results indicate that pseudoalignment is currently the optimal strategy for recovering the relative expression of highly similar gene family members (Author response image 1 C).

Author response image 1

(A) Distribution of pairwise sequence identity values calculated among the 3′-end regions of all transcripts (defined as the 3′UTR plus 20% of the coding sequence). (B) Distribution of read mapping coordinates over all multigene family transcripts normalized as percentage of the gene length (C) Scatter plots showing the correlation between estimated transcript counts obtained using kallisto (red) and STAR + featureCounts (grey) versus the corresponding simulated ground-truth values.

Reviewer #2 (Public review):

Summary:

This manuscript presents a valuable single-cell RNA-seq study on Trypanosoma cruzi, an important human parasite. It investigates the expression heterogeneity of surface proteins, particularly those from the trans-sialidase-like (TcS) superfamily, within amastigote and trypomastigote populations. The findings suggest a previously underappreciated level of diversity in TcS expression, which could have implications for understanding parasite-host interactions and immune evasion strategies. The use of single-cell approaches to delve into population heterogeneity is strong. However, the study does have some limitations that need to be addressed.

The focus on single-cell transcriptional heterogeneity in surface proteins, especially the TcS family, in T. cruzi is novel. Given the important role of these proteins in parasite biology and host interaction, the findings have potential significance.

Strengths:

The key finding of heterogeneous TcS expression in trypomastigotes is well-supported. The analysis comparing multigene families, single-copy genes, and ribosomal proteins highlights the unusual nature of the variation in surface protein-coding genes.

Weaknesses:

While the manuscript identifies TcS heterogeneity, the functional implications of the different expression profiles remain speculative. The authors state it may reflect differences in infectivity, but no direct experimental evidence supports this.

The manuscript lacks any functional validation of the single-cell findings. For instance, do the trypomastigote subpopulations identified based on TcS expression exhibit differences in infectivity, host cell tropism, or immune evasion? Such experiments would greatly strengthen the study.

We thank the reviewer for their careful reading of the manuscript. We agree that obtaining experimental evidence on the influence of multiple multigene families would represent a significant advancement in the field. However, we would like to emphasize that this study is presented as a short communication centered on a specific and biologically relevant observation within a single multigene family. The aim of the manuscript is to highlight what we consider an important biological phenomenon that raises hypotheses to be tested in future work.

The influence of phenotypic heterogeneity and its possible advantages under environmental pressures has been previously proposed for Trypanosoma cruzi, related trypanosomatids, and other biological systems, ranging from bacteria to tumors (Seco-Hidalgo 2015, doi: 10.1098/rsob.150190 and Luzak 2021, doi: 10.1146/annurev-micro-040821-012953, for a comprehensive review on this topic). While the reviewer is correct in noting that our model does not demonstrate a functional role for TcTS heterogeneity, the experimental approaches required to address this question in a large multigene family are highly complex. This is particularly challenging in T. cruzi, where the study of multigene families is limited by the restricted set of available molecular biology tools (such as RNAi). Therefore, further experimental validation of these observations falls outside the scope of this short report.

In this revised version, we have included additional validation and clarification of the results, as well as a more explicit discussion of their limitations. In addition, we present a preliminary analysis exploring potential mechanisms that could coordinate the observed expression patterns of the TcTS family.

The authors identify a subpopulation of TcS genes that are highly expressed in many cells. However, it is unclear if these correspond to previously characterized TcS members with specific functions.

The TcS subgroup with a high frequency of detection comprises 31 genes, none of which belong to the catalytically active Group I trans-sialidases. Instead, this subgroup includes members of Groups II, III, IV, V, VI, and VIII. This information has been added to Supplementary Table 3 and is now stated in the revised manuscript.

The authors hypothesize that observed heterogeneity may relate to chromatin regulation. However, the study does not directly address these mechanisms. There are interesting connections to be made with what they identify as the colocalization of genes within chromatin folding domains, but the authors do not fully explore this. It would be insightful to address these mechanisms in future work.

In response to the reviewer’s and editorial team’s request for additional mechanistic insight into the regulatory processes that may be involved in the observed patterns, we have expanded the revised manuscript to discuss how the genomic context of TcS loci could contribute to the observed heterogeneity in TcS expression. As noted in the original version of the manuscript, TcS genes and other surface-protein gene families are largely partitioned into discrete genomic compartments, whose expression has been reported to be regulated by epigenetic control of chromatin-folding domains (doi.org/10.1038/s41564-023-01483-y). However, we previously showed that TcS genes detected in a high proportion of cells are, in most cases, dispersed throughout the genome, arguing against a model in which their preferential expression results from colocalization within a small number of ubiquitously activated chromatin domains. In response to the reviewer’s suggestion, we performed a more detailed analysis of the genomic locations of these TcS genes. We found that many of them are localized within the core compartment (new Figure 5). Because the core compartment is enriched for conserved, housekeeping genes that typically display more constitutive expression (doi.org/10.1038/s41564-023-01483-y), whereas the disruptive compartment is enriched for lineage-specific multigene families associated with variable, stage-specific, and recently reported stochastic expression (doi.org/10.1038/s41467-025-64900-2), our results are consistent with a model in which compartment-specific regulatory mechanisms (in addition to post-transcriptional regulation) influence the differential cellular expression of core- versus disruptive-located TcS genes. We have incorporated these results and discussion in the revised manuscript.

The merging of technical replicates needs further justification and explanation as they were not processed through separate experimental conditions. While barcodes were retained, it would be informative to know how well each technical replicate corresponds with the other. If both datasets were sequenced on the same lane, the inclusion of technical replicates adds noise to the analysis.

Regarding technical details, we now include the total number of mapped reads and average number of reads mapped per cell (new paragraph in the Methods section.

The technical replicates consist of a single Illumina library that was sequenced in two separate runs. As this approach is expected to be highly reproducible, we merged both runs into a single count table. To support this decision, we assessed the concordance between the two sequencing runs and observed an almost perfect correlation between them (Author response image 2).

Author response image 2.

Correlation analysis of number of reads assigned to cells between technical replicate 1 and technical replicate 2.

While the number of cells sequenced (3192) seems reasonable, it's not clear how much the conclusions are affected by the depth of sequencing. A more detailed description of the sequencing depth and its impact on gene detection would be valuable.

We detected a mean of 1088 genes per cell. Based on the 15,319 annotated protein-coding genes in the reference genome, this represents 7.1% of the T. cruzi protein-coding gene complement detected in each cell.

Across the entire dataset, a total of 14,321 genes were detected in at least one cell, representing 93.5% of all annotated protein-coding genes. This suggests that our experiment captured a broad representation of the parasite's transcriptome.

This per-cell detection rate is characteristic of droplet-based scRNA-seq and is consistent with other trypanosomatid studies. For example, the T. brucei single-cell atlas (Hutchinson et al., 2021) reported a median detection of 1052 genes per cell. In the case of T. cruzi, the recently published pre-print of the T. cruzi single cell atlas from Laidlaw & García-Sánchez et al. reported a mean between 298 and 928 genes detected per cell (depending on the sample).

This information is now included in Methods.

While most of the methods are clear, the way in which the subsampled gene lists were generated could be more thoroughly described, as some details are not clear for the subsampling of single-copy genes.

The subsampling method was originally described in the Figure 2 legend; to better highlight this approach, we have now moved its description to the Methods section.

Some of the figures are difficult to interpret. For example, the color scaling in the heatmap of Supplementary Figure 3B is not self-explanatory and it is hard to extract meaningful conclusions from the graph.

We agree with the reviewer in this assessment. We have now modified the figures to be more self-explanatory and better reflect the conclusions.

Reviewer #3 (Public review):

The study aimed to address a fundamental question in T. cruzi and Chagas disease biology - how much variation is there in gene expression between individual parasites? This is particularly important with respect to the surface protein-encoding genes, which are mainly from massive repetitive gene families with 100s to 1000s of variant sequences in the genome. There is very little direct evidence for how the expression of these genes is controlled. The authors conducted a single-cell RNAseq experiment of in vitro cultured parasites with a mixture of amastigotes and trypomastigotes. Most of the analysis focused on the heterogeneity of gene expression patterns amongst trypomastigotes. They show that heterogeneity was very high for all gene classes, but surface-protein encoding genes were the most variable. In the case of the trans-sialidase gene family, many sequence variants were only detected in a small minority of parasites. The biology of the parasite (e.g. extensive post-transcriptional regulation) and potential technical caveats (e.g. high dropout rates across the genome) make it difficult to infer what this might mean for actual protein expression on the parasite surface.

We thank the reviewer for this important comment, highlighting a central challenge when studying trypanosomatid biology. We acknowledge that in most eukaryotes and particularly in T. cruzi, where there is a predominant role of post-transcriptional regulation, mRNA levels are not always directly correlated with protein abundance, as previously reported by us and others (10.1186/s12864-015-1563-8, 10.1128/msphere.00366-21, 10.1590/S0074-02762011000300002, 10.1042/bse0510031). Nevertheless, steady-state transcript levels obtained by RNA-seq remain informative for assessing differential gene expression, and this approach has been widely used as a proxy for the study of gene expression profiles in T. cruzi (10.7717/peerj.3017, 10.1371/journal.ppat.1005511, 10.1016/j.jbc.2023.104623, 10.3389/fcimb.2023.1138456, 10.1186/s13071-023-05775-4).

It's also interesting to note that recent proteomic analyses (10.1038/s41467-025-64900-2) have revealed substantial heterogeneity in the expression of surface proteins, including trans-sialidases, supporting the idea that the transcriptional heterogeneity we observe reflects a genuine biological feature that propagates to the protein level.

We have now added a sentence to the discussion acknowledging this limitation and discussed the results from Cruz-Saavedra, et al. in the revised manuscript.

(1) Limit of detection and gene dropouts

An average of ~1100 genes are detected per parasite which indicates a dropout rate of over 90%. It appears that RNA for the "average" single copy 'core' gene is only detected in around 3% of the parasites sampled (Figure 2c: ~100 / 3192). This may be comparable with some other trypanosome scRNAseq studies, but this still seems to be a major caveat to the interpretation that high cell-to-cell variability in gene expression is explained by biological rather than technical factors. The argument would be more convincing if the dropout rates and expression heterogeneity were minimal for well-known highly expressed genes e.g. tubulin, GAPDH, and ribosomal RNAs. Admittedly, in their Final Remarks, the authors are very cautious in their interpretation, but it would be good to see a more thorough discussion of technical factors that might explain the low detection rates and how these could be tested or overcome in future work.

(2) Heterogeneity across the board

The authors focus on the relative heterogeneity in RNA abundance for surface proteins from the multicopy gene families vs core genes. While multicopy gene sequences do show more cell-to-cell variability, the differences (Figure 2D) are roughly average Gini values of 0.99 vs 0.97 (single copy) or 0.95 (ribosomal). Other studies that have applied similar approaches in other systems describe Gini values of < 0.2-0.25 for evenly expressed "housekeeping" genes (PMIDs 29428416, 31784565). Values observed here of >0.9 indicate that the distribution for all gene classes is extremely skewed and so the biological relevance of the comparison is uncertain.

We recognize the limitations imposed by gene dropout in our data, as highlighted by the reviewer. Unfortunately, gene dropout is an inherent limitation of 10x genomics data. Trypanosomatids are not an exception in this regard, and the general metrics of the single-cell RNA-seq data in other reports are equivalent to those obtained in our experiment.

Despite this important limitation, we believe that our comparative analyses (the contrast between TcS and ribosomal protein expression) provide valuable insights into a biological phenomenon with potential functional relevance for the parasite. Furthermore, we are actively working on generating single-cell RNA-seq data using alternative methodologies that improve gene dropout rates. We anticipate that these future studies will help clarify the extent of the phenomenon described in this work.

Our results reveal a small subset of TcS genes that are frequently detected across cells, a pattern that is not compatible with random detection unless these genes were highly expressed and preferentially captured by random sampling. However, as shown in Figure 4b, many genes expressed at comparable levels are not detected at high frequencies. In line with this, Figure 4c shows that within individual cells, the detected TcS genes exhibit similar expression levels. Finally, we confirmed that this frequently detected subset shows high read counts at the bulk RNA-seq level (Figure 4 - Figure Supplement 1), consistent with the fact that these TcS are frequent in the population even when they are not specially highly expressed within each cell. Taken together, these findings argue against a purely random sampling of TcS genes and support the interpretation that this pattern reflects an underlying biological feature. We agree that further validation will be required. Accordingly, since the initial submission, we have been careful to frame our conclusions conservatively, explicitly noting that dropout remains a limitation of these data that could influence the observed patterns. In the revised version, we have strengthened this point by including a specific statement in the final remarks. Our interpretation is presented as a working hypothesis that is fully compatible with the observations reported here and may be informative for the field. To better reflect this reasoning, we have revised Figure 4b, expanded the discussion, and explicitly included this limitation in the final remarks of the revised manuscript.

Nevertheless, this study does provide some tantalising evidence that the expression of surface genes may vary substantially between individual parasites in a single clonal population. The study is also amongst the very first to apply scRNAseq to T. cruzi, so the broader data set will be an important resource for researchers in the field.

We thank the reviewer for highlighting the relevance of our study and for their positive assessment of the potential significance of these observations. We also agree that the dataset generated here may represent a useful resource for the community.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) In Figures 1c and 1d, it would be useful to include the genes as the plot titles.

We agree with the reviewer that including gene names in the plot makes the panels more self-explanatory. We have added gene names to the updated version of Figure 1.

(2) Can you include the read lengths of the sequencing and whether this is sufficient to map accurately to very similar genes of the same multigene family? As stated in the public summary, this would make the data far more convincing as standard 10x chromium cannot distinguish similar gene copies unless a longer read 2 is used. Given that only the 3' end is targeted, is this enough to distinguish the TcS and other mutligene family transcripts?

We thank the reviewer for raising this important point. We agree that short 3′ biased reads can limit the disambiguation of highly similar multicopy transcripts. This is, in fact, a common challenge when analyzing transcriptomic data from T. cruzi.

To address this issue, we analyzed the sequence identity of the 3′ ends of TcS transcripts (defined as the 3′UTR plus 20% of the CDS region). As shown in Author response image 1, these regions display a median sequence identity of approximately 25%, indicating that sufficient sequence divergence exists for mapping algorithms to use during read assignment.

In addition, it is important to note that kallisto, the software used in our analysis, was specifically designed to address multimapping reads through pseudoalignment combined with an expectation-maximization algorithm that probabilistically assigns reads across compatible transcripts.

To directly assess performance, we simulated reads from the T. cruzi transcriptome used in this study (3′UTRs plus 20% of the CDS regions) and compared two mapping/counting strategies: (a) transcriptome pseudoalignment using kallisto, and (b) genome alignment followed by counting using STAR + featureCounts. The latter approximates the strategy implemented in CellRanger, the standard pipeline for quantifying expression levels from 10X Genomics single cell RNA-seq data. We found that kallisto recovered the simulated “true” counts with substantially higher accuracy than STAR + featureCounts (Pearson correlation: all genes, 0.991 vs 0.595; surface protein genes, 0.9996 vs 0.827; trans-sialidase (TcS) genes, 0.9998 vs 0.773). These results indicate that pseudoalignment is currently the optimal strategy for recovering the relative expression of highly similar gene family members (Author response image 1C).

The length of the R2 read (91bp) was included in Methods (line 411).

(3) It is stated that 'single copy' genes also include 'low copy number genes". What does this include exactly? Is it more actuate to say non-surface protein genes?

The distinction we aim to make is between multigene families and the rest of the genome. Most multigene families encode surface proteins, but not all surface protein genes belong to multigene families. To clarify this point we included a sentence in methods to reflect that when we describe “surface proteins” we are referring to surface proteins coded by multigene families (line 453). In addition, long-read genomic DNA sequencing and assembly have revealed that many genes previously believed to be single-copy are actually duplicated at low copy numbers (doi.org/10.1099/mgen.0.000177). For this reason, we extend the concept of “single-copy” genes to include those that have only a few duplicates.

(4) It is stated in line 127 that TcS have particular high heterogeneity - it does not look that way by eye compared to the other multigene families. Can statistic be used to prove this, or simply state the decision was made to focus on the TcS?

As noticed by the reviewer, all multigene families show significantly higher heterogeneity compared to single-copy genes, as stated in the text and shown in figure legends from Figure 2, Supplementary Figure 1 and the new Supplementary Table 2.

That said, it was not the statistical results that guided our decision to focus on TcS, but rather their well-established biological relevance in T. cruzi. As suggested, we have now emphasized this rationale more clearly in the revised text (lines 160-167).

Besides, recent work has shown that TcS genes exhibit a bimodal distribution of expression levels using bulk RNA-seq data, in contrast to core genes and other multigene families (doi.org/10.1038/s41467-025-64900-2, doi.org/10.1038/s41564-023-01483-y). This distinct regulatory behavior further justifies our decision to examine TcS separately.

(5) Expression of different TcS has been investigated between the different life cycle stages for a few individual genes previously (Freitas et al). Can the authors not extend this investigation to all the genes detect by scRNA-seq here to demonstrate those with higher/lower expression in amastigotes vs trypomastigotes building on Figure 2A? Are particular groups linked to either stage?

We performed this analysis and did not observe any correlation between TcS groups and life cycle stage. In all cases TcS were more frequently detected in trypomastigotes. This difference was statistically significant for all groups except group VII, likely due to the low number of genes analyzed in this group (Author response image 3).

Author response image 3.

Per-gene number of expressing cells by TcS group and life-stage. Boxplots show, for each TcS group (I–VIII), the distribution across genes of the number of cells in which the gene is detected. Each point represents a single TcS; Amastigote cells: green points/boxes, Trypomastigote cells: salmon points/boxes. The y-axis is on log10 scale. Asterisks indicate statistically significant differences from the comparison between Amastigote and Trypomastigote within each TcS group, assessed using a paired two-sided Wilcoxon signed-rank test: * p < 0.05, ** p < 0.01, *** p < 0.001.

(6) What exactly is the Z-score shown in Figure 2B?

In this analysis num_multigene represents the number of multigene family genes detected in each individual cell. For every cell, we counted how many genes from our predefined multigene family gene list has detectable expression (more than zero UMI counts); in the UMAP plot, this value is reflected by the size of each point. On the other hand, z_multigene captures the relative expression level of multigene family genes within each cell. This metric is calculated by summing the UMI counts of all multigene family genes per cell and then standardizing this value across the dataset using a z-score transformation, such that positive values reflect above-average multigene family expression and negative values reflect below-average levels. In the UMAP plot, this metric determines the color scale of each point. Taking together num_multigene and z_multigene allow us to distinguish cells that express multigene family genes broadly (high gene counts), strongly (high relative expression), both, or neither, and to relate these patterns to identified cell populations.

We included a short description in legend of the new version of Figure 2 (lines 176-180).

(7) For the reclustering of trypomastigotes based on TcS genes alone, please show the UMAP and discuss why the resolution giving two clusters is chosen? I assume increasing the resolution does not reveal clusters of cells express one of the 8 groups of TcS for example?

We appreciate the reviewer’s suggestion. In this analysis, our goal was to test whether the phenotypic heterogeneity previously reported in trypomastigotes could be recapitulated using TcS genes alone, as prior studies described two major transcriptomic phenotypes within this stage.

Increasing the clustering resolution did not reveal subclusters corresponding to the eight TcS sequence groups. This might reflect the fact that these groups are defined based on sequence similarity rather than on expression patterns, as noted by Freitas et al. (doi:10.1371/journal.pone.0025914).

(8) In Figure 4B, there may be an upward trend in the level of expression and the number of cells a transcript is detected in? It would be worth showing this is or is not the case with statistics if possible.

The number of genes detected in a high proportion of cells is low, which limits the statistical power of this analysis. Also, substantial dispersion is observed within the 0-5% interval. Nevertheless, this figure is presented primarily to highlight that a considerable number of highly expressed genes are detected in only a small fraction of cells. If expression level were the main determinant of detection frequency across cells, one would expect very few highly expressed genes to fall within the 0-5% interval. Contrary to this expectation, among the 50 highest expressed TcS genes, 62% are detected in fewer than 5% of cells, and even among the top 10 most highly expressed TcS genes, 40% fall within this lowest detection group. To facilitate this interpretation, we modified the figure (new Figure 4b) to explicitly highlight the top 50 most expressed TcS genes and incorporated this discussion into the main text of the revised manuscript (lines 244-251), making the conclusion clearer to the reader.

(9) Do the cells group instead by expression of any of the other multigene families not investigated in detail?

It is possible that additional transcriptional substructure among trypomastigotes is driven by the expression of other multigene families beyond TcS. In this short report (with limited number of figures, words, etc.), we focused specifically on the trans-sialidase family as discussed earlier. A more comprehensive analysis including other large surface gene families (MASPs, mucins, GP63) is planned as part of ongoing work and will be presented in future reports.

Reviewer #2 (Recommendations for the authors):

This reviewer suggests the conduction of functional experiments in follow-up studies to establish links between TcS expression profiles and parasite behavior and into potential regulatory mechanisms responsible for the observed TcS heterogeneity, particularly focusing on epigenetic modifications. It would be interesting to correlate the highly expressed TcS members identified here with previously characterized TcS isoforms and provide more description regarding which particular groups and TcS members are driving the findings. It would benefit from further clarification regarding sequencing depth, technical replication merging, subsampling, and specific parameters for alignment methods and more information regarding the specific statistical tests and their applicability to the data.

This is a promising single-cell study with potentially high significance. The manuscript is well-written, and the analyses are reasonably well-executed. However, the current manuscript is limited by a lack of functional validation and mechanistic insights. The addition of further analyses and experiments, as suggested, will strengthen the conclusions and increase the impact of the work.

We thank the reviewer for their careful reading of the manuscript. As suggested, we have performed additional validation and clarification of the results, as well as a more explicit discussion of their limitations. In addition, we have included a preliminary analysis exploring potential mechanisms that could be coordinating the observed expression patterns of the TcS family (see below). Even though we consider relevant and interesting to experimentally validate these results, given the inherent difficulties in studying multigene families in T. cruzi, an organism with a very limited set of molecular biology tools (such as RNAi), further experimental validation of these observations is outside of the scope of this short report.

Regarding the reviewer’s question, we studied if any TcS subgroup could be driving our observations. However, we did not find any correlations indicating that a particular group was associated with any of our findings. We now include TcS group information to Supplementary Table 3.

Regarding technical details, we now included the total number of mapped reads (line 422) and average number of reads mapped per cell (new paragraph in the Methods section, line 432-436).  

The technical replicates consist of a single Illumina library that was sequenced in two separate runs. As this approach is expected to be highly reproducible, we merged both runs into a single count table, as stated in line 424. To support this decision, we assessed the concordance between the two sequencing runs and observed an almost perfect correlation between them (Author response image 2).

The subsampling method was originally described in the Figure 2 legend; to better highlight this approach, we have now moved its description to the Methods section (line 456).

The specific kallisto parameters used are stated in Methods (line 418-419). We now included that default options were used unless otherwise specified (line 419-420).

In response to the reviewer’s and editorial team’s request for additional mechanistic insight into the regulatory processes that may be involved in the observed patterns, we have expanded the revised manuscript to discuss how the genomic context of TcS loci could contribute to the observed heterogeneity in TcS expression. As noted in the original version of the manuscript, TcS genes and other surface-protein gene families are largely partitioned into discrete genomic compartments, whose expression has been reported to be regulated by epigenetic control of chromatin-folding domains (doi.org/10.1038/s41564-023-01483-y). However, we previously showed that TcS genes detected in a high proportion of cells are, in most cases, dispersed throughout the genome, arguing against a model in which their preferential expression results from colocalization within a small number of ubiquitously activated chromatin domains. In response to the reviewer’s suggestion, we performed a more detailed analysis of the genomic locations of these TcS genes. We found that many of them are localized within the core compartment (new Figure 5). Because the core compartment is enriched for conserved, housekeeping genes that typically display more constitutive expression (doi.org/10.1038/s41564-023-01483-y), whereas the disruptive compartment is enriched for lineage-specific multigene families associated with variable, stage-specific, and recently reported stochastic expression (doi.org/10.1038/s41467-025-64900-2), our results are consistent with a model in which compartment-specific regulatory mechanisms (in addition to post-transcriptional regulation) influence the differential cellular expression of core- versus disruptive-located TcS genes. We have incorporated these results and discussion in line 301-313 of the revised manuscript.

Reviewer #3 (Recommendations for the authors):

(1) The authors consistently refer to gene "expression" but somewhere they should acknowledge that in trypanosomes RNA abundance is less predictive of protein than in most other organisms.

We thank the reviewer for this important comment, highlighting a central challenge when studying trypanosomatid biology. We acknowledge that in most eukaryotes and particularly in T. cruzi, where there is a predominant role of post-transcriptional regulation, mRNA levels are not always directly correlated with protein abundance, as previously reported by us and others (10.1186/s12864-015-1563-8, 10.1128/msphere.00366-21, 10.1590/S0074-02762011000300002, 10.1042/bse0510031). Nevertheless, steady-state transcript levels obtained by RNA-seq remain informative for assessing differential gene expression, and this approach has been widely used as a proxy for the study of gene expression profiles in T. cruzi (10.7717/peerj.3017, 10.1371/journal.ppat.1005511, 10.1016/j.jbc.2023.104623, 10.3389/fcimb.2023.1138456, 10.1186/s13071-023-05775-4).

It's also interesting to note that recent proteomic analyses (10.1038/s41467-025-64900-2) have revealed substantial heterogeneity in the expression of surface proteins, including trans-sialidases, supporting the idea that the transcriptional heterogeneity we observe reflects a genuine biological feature that propagates to the protein level.

We have now added a sentence to the discussion acknowledging this limitation and discussed the results from Cruz-Saavedra, et al. in linea 266-271 of the revised manuscript.

(2) Line 29, in the abstract there is a strong statement that T. cruzi "does not employ antigenic variation". I don't think there is much evidence either way if we are thinking about antigenic variation in the broad sense rather than the extreme model of T. brucei VSG switching. Later in the abstract they state that "no recurrent combinations of TcS genes were observed between individual cells in the population", which sounds very much like a form of antigenic variation.

We agree with the reviewer. Indeed, we meant to state that T. cruzi does not employ an antigenic variation mechanism such as the one from T. brucei. We change this statement as suggested in lines 28 - 32.

(3) Line 29, "relies on a diverse array of cell-surface-associated proteins encoded by large multi-copy gene families (multigene families) essential for infectivity and immune evasion" and lines 55-58 "T. cruzi infection relies on a heterogeneous set of membrane proteins, encoded mainly by large multigene families ... most of which are involved in infection, tropism, and immune evasion". It would be worth adding a bit more detail on the nature and strength of the evidence that Tc "relies on" these various genes or that they are "essential" for infectivity, tropism, and immune evasion.

Because the journal’s short format imposes word limits, we strengthened the original statement by adding specific references that document genomic, transcriptomic and functional evidence linking the major multigene families to infectivity, tropism and immune evasion (doi.org/10.1371/journal.pone.0025914; doi.org/10.1038/nrmicro1351; doi.org/10.1128/iai.05329-11; doi.org/10.1093/nar/gkp172, doi.org/10.1371/journal.ppat.1006767), in line 77.

(4) Line 89, 1088 genes detected per cell - what is this as a % of genes in the genome?

We detected a mean of 1088 genes per cell. Based on the 15,319 annotated protein-coding genes in the reference genome, this represents 7.1% of the T. cruzi protein-coding gene complement detected in each cell.

Across the entire dataset, a total of 14,321 genes were detected in at least one cell, representing 93.5% of all annotated protein-coding genes. This suggests that our experiment captured a broad representation of the parasite's transcriptome.

This per-cell detection rate is characteristic of droplet-based scRNA-seq and is consistent with other trypanosomatid studies. For example, the T. brucei single-cell atlas (Hutchinson et al., 2021) reported a median detection of 1052 genes per cell. In the case of T. cruzi, the recently published pre-print of the T. cruzi single cell atlas from Laidlaw & García-Sánchez et al. reported a mean between 298 and 928 genes detected per cell (depending on the sample).

This information is now included in Methods (line 435).

(5) Line 93-94, how many cells were assigned to clusters 0 and 1?

Cluster 0 had 2201 cells and cluster 1 had 824 cells assigned.  We have now included these specific numbers in new version of the manuscript (line 114).

(6) Line 96, cluster 2 ama-trypo transitioning parasites - were these observable by microscopy?

We did not perform microscopy specifically to observe or quantify the putative ama/trypo transitioning subpopulation: microscopy was only used as a pre-experiment quality check to verify cell morphology and viability. The inference that cluster 2 reflects ama/trypo transitioning parasites is drawn from the transcriptomic profile (particularly from the pattern of stage-associated marker expression observed in that cluster) and should be considered a hypothesis generated by the data, that merits further analysis, as stated in the manuscript.

(7) Line 106-107, "As expected, single-copy gene expression is high in both amastigotes and trypomastigotes and similar on average between both cell types".

(8) Why as expected? For a broad journal it would be useful to explain this. Amastigotes are replicative and trypomastigotes are not, so would we not expect to see some differences that reflect this?

(9) What do you mean by the expression being "high"? High compared to what?

(10) "Similar on average between both cell types". This does not seem concordant with Figure 1a showing a highly significant difference between ama and trypo.

We thank the reviewer for this helpful request for clarification for broader readers and the observations regarding global expression of single copy and multigene family genes.

Figure 2a is intended as an experimental control where we show that our 10X Genomics data shows the previously reported upregulation of surface protein genes in trypomastigotes. We have now modified the text in order to highlight this (line 129). In turn, Supplementary Figure 1a is shown as a control that this upregulation is not a general feature of trypomastigote cells.

Regarding comment 9, what we meant is that single-copy genes display relatively high expression in both amastigotes and trypomastigotes compared with surface protein-coding genes (see expression values in Figures 2a and Supplementary Figure 1a).

Finally, differential expression between amastigotes and trypomastigotes at the transcriptomic level has been previously studied and has shown that most single copy genes do not show variation, explaining the overall pattern of Supplementary Figure 1a where average expression is similar between stages (mean fold change = 1.1). This is likely due to the fact that these genes are related to basic cellular functions. Genes related to stage specific functions such as replication in amastigotes or normalization effects may be causing the slight, but statistically significant increase observed in overall expression in amastigotes. This contrasts with the pattern observed for multigene families where there is a clear overexpression in trypomastigotes (mean fold change = 1.5).

As observations commented on questions 9 and 10 have been described in previous studies and are not novel nor key points in our results, we decided not to focus on them and modified the text accordingly in lines 129-135.

(11) Line 110, "with high variation". What does "high variation" mean here? Compared to what? For the two metrics (n cells +ve for each gene and total expression level) can they give an average and the SD? It would be useful to know how many parasites the "average" surface (and core) gene is expressed in, or more precisely for which the RNA is above the limit of detection.

We refer to the comparison with the expression profile observed for single-copy genes. This point has now been clarified in the text, and we have included the mean and standard deviation for both TcS multigene family genes and single-copy genes in trypomastigotes for both metrics in the Figure 2 legend. The average and distribution of the number of cells in which each gene is detected are shown in Figure 2c and Supplementary Figure 1a. We also added a reference to this panel at the point in the text where the phenomenon is first described.

(12) Line 134, Figure 2b legend needs more detail - what are num_multigene and z_multigene?

Please see our response to Reviewer 1, Question 6. We have now added a clarification to the legends of Figure 1 and Supplementary Figure 1.

(13) Figure 2c, correct the y-axis legend because it implies your values are log10 transformed. Also, it would be useful to have more markers on the y axis so the reader can better estimate the data ranges.

We thank the reviewer for this observation. We have now corrected the y-axis label and markers.

(14) If the y-axis of Figure 2D started at 0 instead of 0.8 and if Lorenz curves were provided then the reader would probably get a fuller sense of the expression heterogeneity in the dataset. The legend states the differences are statistically significant but the actual p-values are not shown.

(15) Line 142-3, more precision is needed on the p-values.

We thank the reviewer for this helpful suggestion. We agree that Lorenz curves provide a clearer representation of expression heterogeneity than the previous plot. Accordingly, we have replaced the original panel (Figure 2d) with Lorenz curves for the groups under comparison, and have made the same change in Supplementary Figure 1d. In addition, we have included gini index values and p-values for all comparisons in Supplementary Table 2.

(16) Figure 3, as in Figure 1a it would be useful to add another UMAP plot to show the two trypo subpopulations.

We thank the reviewer for this suggestion. We have now updated Figure 3 to include a UMAP plot showing the two trypomastigote subpopulations.

(17) What is the observed proportion of broad vs slender trypomastigote morphologies for Dm28c? To be consistent with the speculation at line 162 then wouldn't it need to be approximately 50-50?

The proportions of each trypomastigote subpopulation in the DM28c strain are currently unknown. The only available relevant data come from Brener, 1965 (doi.org/10.1080/00034983.1965.11686277), in which this strain was not included. In the strains analyzed in that study, the relative proportions of broad and slender trypomastigote morphologies were highly variable: across seven strains, broad forms ranged from 18.0% to 77.3%, while slender forms ranged from 2.3% to 71.6%. Given this wide variability and the lack of DM28c-specific data, we cannot assume any expected proportion for this strain.

(18) Line 170, please state how many genes are in the TcS subgroup mentioned here. This is an interesting finding - does this include mostly catalytically active trans-sialidase genes or is it a mixture from across all the subfamilies?

The TcS subgroup with a high frequency of detection comprises 31 genes, none of which belong to the catalytically active Group I trans-sialidases. Instead, this subgroup includes members of Groups II, III, IV, V, VI, and VIII. This information has been added to Supplementary Table 3 and is now stated in the revised manuscript (lines 227 - 228).

(19) Line 175-176, "Gene dropouts might favor random patterns of gene family's detection in scRNA-seq experiments, particularly affecting genes with low expression" - I'm not sure if the authors mean the detection of a gene (or not) in an individual parasite is truly random (pure luck) or whether the term stochastic would be more appropriate because they seem to be referring to randomness around a certain threshold of RNA abundance/stability? They go on to rule this out, at least for TcS genes, essentially arguing that they have something resembling an ON or OFF pattern rather than a spectrum of expression levels. This is potentially very important and could advance the field in a major way, but the fact that so many core and ribosomal genes, which 'should' be always ON, cannot be detected in most cells is a concern. A version of Figure 4B for core and ribosomal genes could be informative - do they show a different pattern to TcS?

Our results reveal a small subset of TcS genes that are frequently detected across cells, a pattern that is not compatible with random detection unless these genes were highly expressed and preferentially captured by random sampling. However, as shown in Figure 4b, many genes expressed at comparable levels are not detected at high frequencies. In line with this, Figure 4c shows that within individual cells, the detected TcS genes exhibit similar expression levels. Finally, we confirmed that this frequently detected subset shows high read counts at the bulk RNA-seq level (Supplementary Figure 2), consistent with the fact that these TcS are frequent in the population even when they are not specially highly expressed within each cell. Taken together, these findings argue against a purely random sampling of TcS genes and support the interpretation that this pattern reflects an underlying biological feature. We agree that further validation will be required. Accordingly, since the initial submission, we have been careful to frame our conclusions conservatively, explicitly noting that dropout remains a limitation of these data that could influence the observed patterns. In the revised version, we have strengthened this point by including a specific statement in the final remarks. Our interpretation is presented as a working hypothesis that is fully compatible with the observations reported here and may be informative for the field. To better reflect this reasoning, we have revised Figure 4b, expanded the discussion, and explicitly included this limitation in the final remarks of the revised manuscript.

(20) Line 238-9, Add details of removing extracellular epimastigotes after cell infections.

Only cellular trypomastigotes collected from the supernatant on day 6 were used for the secondary infection, at a 10:1 parasite-to-cell ratio. After 24 hours, the cultures were washed twice with PBS to remove any remaining extracellular parasites. Under these conditions, i.e. using exclusively trypomastigotes, at this infection ratio, and maintaining the cultures in mammalian medium, we do not expect the presence or survival of extracellular epimastigotes. We have included a sentence in the Methods section clarifying this information in the revised version of the manuscript, line 382.

(21) Line 260, was methanol used to directly resuspend the parasite pellet, or was it resuspended first e.g. in a small volume of PBS?

As described in lines 250-257 of the original manuscript, parasites were washed and resuspended in DPBS before methanol fixation. Methanol fixation was then carried out according to the 10X Genomics Methanol Fixation Protocol. We have now emphasized this more clearly in the revised text in line 400.

(22) What was the doublet rate?

We identified and removed 41 doublets, all belonging to cluster 2, and retained 3,151 singlets for downstream analysis (total cells before removal = 3,192). The resulting doublet rate was 1.28%. We have included a sentence in the Methods section clarifying this information in the revised version of the manuscript, line 439 -440.

(23) What was the frequency of rRNA and kDNA-derived reads?

Approximately 4.02% of the reads were derived from kDNA sequences, while 1.10% corresponded to rRNA-derived reads (Author response image 4).

Author response image 4.

Percentage of mitochondrial and ribosomal rRNA derived reads.

Author response:

Reviewer #1 (Public review):

We thank the reviewer for the thoughtful and detailed evaluation of our manuscript. We are pleased that the continuous-time formulation and its methodological contributions were viewed as elegant and broadly applicable, and that the empirical analyses provide meaningful new insights into neural variability across the visual hierarchy. We appreciate the reviewer’s constructive suggestions and clarifications, which will help us improve the precision, clarity, and scope of the manuscript. Below we respond to each point in turn and outline the revisions we will make.

(1) Extension to neural populations: We thank the reviewer for this important suggestion. We agree that extending the framework to population recordings is a natural next step. In this work, we focus on single-cell data to establish the model and validate inference. In the revised manuscript, we will expand the Discussion to outline how the framework could be generalized to population activity, for example by incorporating shared latent-variable structure.

(2) Clarification regarding the Modulated Poisson model: We thank the reviewer for pointing this out. We agree that our description was not sufficiently precise and may have been unclear. The modulated Poisson model introduced in Goris et al. (2014) is indeed a generative process model that can be used to generate spike trains, and we apologize for the inaccurate characterization of this framework. Our intended point was that the original formulation assumes gain is constant within a trial (or counting window) and does not provide a principled mechanism for modeling continuously time-varying gain fluctuations within trials. In the revised manuscript, we will clarify this distinction and revise the relevant passages accordingly. We will also cite and discuss related extensions and analyses in Goris et al. (2018) and Hénaff et al. (2020) to provide a more accurate and complete characterization of prior work.

(3) Continuous extensions of the Goris model: We thank the reviewer for this helpful clarification. We agree that the Goris model is not limited to homogeneous Poisson spiking and can incorporate a stimulus-dependent, time-varying firing rate within trials. We did not intend to imply otherwise, and we will revise the relevant text to avoid this misunderstanding. Our intended point was that, in formulating continuous-time extensions, we explicitly model the time-varying stimulus drive using a GP prior, as in the CMP framework, and then consider different assumptions about the temporal structure of the gain process, including constant and finely sampled gain. This highlights the distinction between piecewise-constant gain assumptions and the fully continuous gain process introduced in our model. We will clarify this distinction in the revised manuscript. We will also acknowledge related variants explored in Hénaff et al. (2020) and more clearly describe how our formulation differs, including the role of smoothness priors on the stimulus drive and gain processes.

(4) Continuous-time extension: We thank the reviewer for the positive comment and are pleased that the continuous-time formulation was viewed as elegant.

(5) Parameter recovery analysis: We thank the reviewer for emphasizing the importance of this result. We agree that demonstrating parameter recoverability is foundational to the paper. In the revised manuscript, we will move the Appendix 3 analysis into the main Results section and clearly illustrate how our inference procedure faithfully recovers the generative parameters in simulation studies.

(6) Validation of gain–stimulus separation: We thank the reviewer for this insightful suggestion. We agree that verifying that the inferred gain does not capture stimulus-driven structure is an important validation of the model. In the revised manuscript, we will compute the trial-averaged inferred gain, to assess whether it exhibits systematic temporal structure. This analysis will provide an additional check that the partitioning between stimulus drive and gain fluctuations operates as intended.

(7) Temporal evolution of gain variability: We thank the reviewer for this valuable suggestion. We agree that examining whether gain variability decreases following stimulus onset is an important and relevant analysis. In the revised manuscript, we will compute the temporal evolution of cross-trial gain variability from the inferred gain traces and assess whether a quenching effect is observed after stimulus onset. If present, we will report and illustrate this result.

(8) Clarification of Baseline Poisson and Poisson-GP models: We thank the reviewer for this careful reading. Yes, this understanding is correct. The Baseline Poisson model uses a stimulus-conditioned PSTH as an estimate of the time-dependent firing rate and includes a Gamma prior to regularize rate estimates in conditions with sparse repeats. The Poisson-GP model retains the same structure but models the time-dependent firing rate using a stimulus-specific Gaussian process prior, which substantially improves goodness-of-fit. In the revised manuscript, we will clarify this description. We will also highlight that Figure 4 – figure supplement 2 illustrates how introducing a GP smoothness prior on the stimulus drive markedly improves model fit, even within the Goris-style model.

Reviewer 2 (Public review):

We thank the reviewer for the thoughtful and positive assessment of our work. We are pleased that the model development, empirical analyses, and presentation were found to be clear and rigorous. We appreciate the recognition that the continuous-time formulation meaningfully extends prior variability-partitioning approaches and enables a more precise characterization of how stimulus drive and internal gain dynamics evolve across temporal scales. We are also encouraged that the cross-area analyses and model comparisons were viewed as providing new insights and clear empirical improvements. Below, we address the specific suggestions raised by the reviewer.

Positioning relative to prior work: Regarding the comment on incremental contribution, we agree that our framework builds directly on earlier variability-partitioning approaches. Our goal was to extend these models to continuous time and to develop a principled inference framework capable of characterizing how gain dynamics evolve across temporal scales. We will further clarify this positioning in the revised manuscript.

Extension to sub-Poisson variability: We thank the reviewer for this suggestion. We agree that sub-Poisson variability is an important phenomenon observed in neural data. Because the CMP model builds on a Poisson observation model with stochastic gain modulation, it naturally captures Poisson and super-Poisson variability but cannot generate sub-Poisson spike count statistics in its existing form. We will clarify this limitation in the revised manuscript and expand the Discussion to outline potential extensions that could address sub-Poisson variability, such as incorporating spike-history effects, renewal-process models, or alternative count distributions.

Author response:

Public Reviews:

Reviewer #1 (Public review):

…It is unclear whether there are any systematic changes in preferences over the course of testing that could explain the observed changes in correlation with neural responses, such as changes due to learning (e.g., flavor nutrient conditioning, relief of neophobia), changes in deprivation state, or habituation to/proficiency with the BAT setup.

For the revision, we will add analysis (including either additional panels for Figure 3 or as a new Figure between what are now Figures 3 & 4) testing the hypothesis that preference changes across testing days are non-random. Concretely, we will test: 1) whether the preference for palatable tastes increase with experience (a result that would make sense given research on neophobia; 2) whether the preference for aversive tastes decrease with experience; and 3) whether absolute consumption of any particular taste changes in a reliable direction from session to session.

A secondary point is whether any changes in preference are attributed to internal individual versus external contextual factors. Both types of variation (i.e., across individuals and across time within an individual) are mentioned in the introduction, but it is not clear what the authors believe about the nature or neural representation of these sources of variation.

While we assume that differences between rats are due to internal factors (given the controlled home-cage environment), we can’t be sure that some subtle, subthreshold (for us as observers) factor impacts taste preferences. Similarly, while changes across time within an individual is categorically within the individual, we cannot be sure whether some subtle facet of their experiences determines how preferences change (as opposed to it being purely internal). We will add prose to the Discussion session on this topic—including citation of Hilary Schiff’s recent work showing nurture-related preference changes as part of this new prose.

With respect to neural data analysis, no individual animal/day data are shown, making it difficult to assess the extent to which differences in correlation match individual differences in preferences and/or changes in preference with time within individuals.

The revision will include Figure panels (with analysis) showing the relationships between individual neural responses and consumption in the first and last BAT tests for 1-2 representative rats.

The correlation analysis is also lacking control for the fact that there is a certain degree of "chance" associated with behavioral and neural measures having matching ranks.

Certainly chance cannot explain our results, which consist mainly of within-rat differences in match (i.e., specific enhancement of that match for the most recent behavioral assessment)—a finding that is all the more surprising given that: 1) 2 weeks separate that behavior test and the electrophysiology session; and that 2) that 2-week gap is only 1-3 days less than the gap using the first behavioral test (that reliably correlates less well with the neural data). Nonetheless, we will add an independent, convergent analysis to the revision, testing whether the observed pattern vanishes when we shuffle the preference ranks in the behavioral data—if the result is based on chance, this shuffling should have no impact on the neural-behavioral match.

Finally, …it is unclear to what extent changes in correlation may be attributed to overall changes in responsiveness of the neural population.

We will include a new analysis in the revision testing the hypothesis that the reduction in match between the neural and behavioral rankings reflects changes in neural excitability—spontaneous and taste-driven—between the first and second electrophysiology sessions.

Reviewer #2 (Public review):

The manuscript could use additional corollary analyses to provide a more complete picture of the phenomenon. For instance, how many neurons (per animal and in total) have significant correlations with the final BAT patterns? And with the first BAT? Can a time course of such counts be provided? Can some decoding analyses be performed at a single session level to reconstruct a rat's behavioral preference pattern from its neural activity?

These are all really good ideas. We are in the process of implementing all but the last; we will attempt the last as well, but can’t promise that we have large enough ensembles to provide stable results of such a subtle decoding task (reflecting the last BAT session’s preference pattern significantly better than the first session’s pattern).

The manuscript could benefit from additional polishing, both in the text as well as in the figures.

It is being done, on the basis of suggestions made by R2 in the non-public comments.

Reviewer #3 (Public review):

Without a behavioral measure collected after recording day 1 intraoral exposure, it is not possible to determine whether taste preference was altered by that experience…The authors' conclusion would be strengthened by adding an intervening brief access test between recording days 1 and 2.

We very much appreciate Reviewer 3’s suggestion, but the primary authors involved in data collection on this project have moved on, and we won’t be able to collect the additional dataset that would be required. Instead, we will soften the conclusion that we reach in the last section, and suggest this experiment as a future direction.

The current experimental design exposes animals to 3 distinct sets of substances … [that] differ in identity … and concentration. Because palatability is known to be comparative depending on the other substances available and concentration-dependent, this introduces challenges to interpretation, [and] without more clarity, it is difficult to evaluate whether the interaction of different tastes within the sets of stimuli biases the main conclusions.

This is an interesting point. We hope that some of the work that we are undertaking in response to Reviewers 1 & 2 (see above) will shed light on whether there is any non-randomness in between-session preference changes; such non-randomness would imply that we might want to conclude that preferences change more with one battery than another. But we will perform a more direct test of this hypothesis, breaking the dataset apart and asking whether our phenomena are observed more with one battery than another. If it turns out that the magnitude of the impact of experience does depend on the nature of the taste battery (we predict not, for reasons that are in the manuscript), we shall introduce that complexity into our interpretation, and the Discussion thereof.

Responses to sweet tastes are not reported in the electrophysiology data. This is seemingly the case because rats given set 1 received no sweet stimulus while rats given set 2 received to 2 distinct sweet tastes. Finally, rats given set 3 did not receive quinine, yet quinine is reported in electrophysiology data.

We are unsure of the source of this confusion—in every case, the rat received the same tastes in the electrophysiology sessions that were delivered in the BAT preference tests—but we will modify the text to ensure: 1) that panels reflecting data from a single rat (panels that will therefore necessarily include only a subset of possible tastes) are clearly marked as such; and 2) that the nature of which taste batteries were delivered is more explicit.

The choice of reporting average lick cluster size is problematic because the authors use thirsty rats with 10-second-long trials. Thirsty rats are likely to lick in relatively long clusters, especially for neutral and palatable tastes. If the rat is mid-cluster when the trial ends, the final cluster would be cut off prematurely, resulting in shorter overall average lick cluster size, disproportionately affecting neutral and palatable tastes over aversive tastes.

We have ourselves been deeply concerned with this issue; we have recently published a paper that includes within it a direct test demonstrating that calculations of lick bout lengths from 10-sec BAT trials result in taste palatability estimates that are identical to (and less noisy than) those generated from more classically-used 15-min ad lib licking. We will cite this paper (Lin, et al., 2026) in the Methods section of the revision, along with text clarifying how we calculated lick clusters. That said, we are also planning to conduct an additional analysis that estimates taste preference after removing these “premature bouts” and will evaluate how this recalculation affects our results.

Of course, even if 10-sec BAT trial data DIDN’T provide reliable preference measures, the result of clusters being cut short by the end of a trial would be an underestimation of the preference for the palatable tastes (which drive far more licking than aversive tastes and are therefore more likely to be mid-bout at the end of a trial). Such an underestimation would in turn be expected to reduce the observed neural-behavioral correlation. This fact actually highlights the robustness of our findings.

Canonical palatability rankings may not apply to the concentrations selected in every stimulus set. This is particularly true for set 1, which included two concentrations of citric acid and quinine for the behavior. It is also not clear which concentrations are reported in Figures 3A2 and 3B2. Meanwhile, the concentrations of quinine and citric acid used for electrophysiology are quite low.

In the revision Methods section, we will explicitly motivate our reasoning behind canonical rankings for each taste battery used (the added text will include citations). We have also added to the Discussion section prose concerning the possible impact of possibly getting those rankings wrong—i.e., the impact is minimal, given that our results are largely driven by differences between rats (and day-to-day differences within rat), and the resultant fact that almost any choice of canonical rankings would poorly reflect the behavior of individual rats on individual days.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors provide extensive immunoreactivity and expression data to map monoaminergic neurotransmitter production sites in Pristionchus pacificus. This nematode is relatively distantly related to the popular model nematode Caenorhabditis elegans, for which such information is already available. They find that dopamine, tyramine, and octopamine are present in the same neurons in both species, but differences are observed for serotonin. This forms the basis for a comparison of serotonergic neurons across 22 nematode species. In addition, they evaluate monoaminergic effects on egg-laying, head movement during reversals, and nictation behavior, to find that monoaminergic control over the latter differs between C. elegans and P. pacificus. This shows that some anatomical flexibility supports similar outcomes, whereas in other cases it is the basis of evolved regulatory differences.

Strengths:

The comparative efforts are laudable and valuable, including a thorough revisiting of old data and corrections of what is judged as a historic misannotation. The expected continued value of this work is also appreciated, because nematodes have similar anatomies and behaviors, cellular-resolution data of different species permits the study of functional evolution of neurotransmitter usage in homologous neurons.

Despite the strong experimental approach, there are some points that require addressing:

(1) Not all the concepts of the introduction ('feeding behaviors', to a lesser extent also 'evolution of neurotransmitter usage in homologous neurons') are followed up upon in the results or discussion sections.

We will address the relative treatment of particular topics in the introduction and discussion in a revised version of the article.

(2) The choice of nematodes ('only' 13 species) may affect what is perceived as ancestral.

See above regarding ‘13 species’ (actually 22). Most species and genera were specifically selected previously (Loer and Rivard, 2007; Rivard et al., 2010) for broad phylogenetic coverage, representing different species and genera in 4 major clades within ‘clade V’ (Kiontke et al., 2007; Sudhaus, 2011): Anarhabditis (Caenorhabditis, including both the Elegans and Drosophilae species groups), Synrhabditis (Oscheius, Metarhabditis, Reiterina and Rhabditella), Pleiorhabditis (Teratorhabditis, Mesorhabditis, Rhomborhabditis and Pelodera), and Diplogastrids represented by P. pacificus. Among the outgroups to clade V, there are 3 distinct clades represented, each with at least two species and/or genera represented. Therefore, we believe that the determination of an ancestral condition is well-founded. We plan to add this rationale to the revised version to make this clearer.

(2, continued) Also, identifying their cells based on comparisons with Ce or Ppa identifications only is understandable but mildly risky: there are many cells in the head, and mistakes would go unnoticed until detailed analysis in each species can provide conclusive evidence.

We agree that there is a mild risk of incorrect identification but believe that appropriate caveats are noted in the text. Furthermore, the recent head EM reconstruction and complete embryonic cell lineage of the P. pacificus (Cook et al., 2025) shows a nearly 1-1 homology correspondence between head neurons (e.g., only a single head neuron is missing in the Ppa head relative to Cel due to altered apoptosis), and a quite high level of conservation of neurite morphology and soma position between Cel and Ppa suggests that identifications are likely correct when examining related nematodes. In cases for which a serotonin-immunoreactive cell is found in the predicted location (and often having apparent associated neurites), its homology to the matching Cel and Ppa cell is the most parsimonious interpretation: otherwise, one cell would have to lose expression and another nearby cell gain it.  

(3) It is not reported whether the nictation-defective mutants have general locomotion defects; therefore, whether the reported problem is specific to this host-finding behavior or not.

None of the mutants we tested for nictation behavior, including those that show severe defects in nictation (Ppa-cat-1, Ppa-tph-1, Ppa-tdc-1, Ppa-tbh-1), exhibited noticeable general locomotion defects either as dauers or non-dauers. Further clarification will be provided in a revised version of the article.

(4) The section on RIP neurons makes sense for Ppa, but not for Ce (dauers in fact have weakened IL2-to-RIP connections) and should be revised. The nictation data also do not support the breadth of the conclusions, which should either be toned down or rephrased as hypothetical.

We plan to address these concerns in a revised version of the article.

(5) The discussion mostly reiterates the results, leaving little room for the author's interpretations and opinions. I would suggest reworking in favor of conceptual discussion.

As noted above, we agree to address the relative treatment of matters in discussion in a revised version of the article.

Reviewer #2 (Public review):

Summary:

This paper makes important contributions to our understanding of how nervous systems evolve, with a particular focus on whether changes in neurotransmitter usage within homologous neurons represent a mechanism for evolutionary adaptation without large-scale changes to circuitry. Comparing the predatory nematode P. pacificus with C. elegans, this study systematically examines monoamine-producing neurons, assesses how their neurotransmitter identities differ between homologous neural types, and determines how these differences relate to behavior.

Strengths:

The major strength of this work is its breadth, rigor, and data quality. It combines multiple, independent lines of evidence to assign neurotransmitter identity for neurons with homology grounded in lineage, morphology, and connectomics, which is essential for meaningful cross-species comparisons. Additionally, by extending the analysis beyond P. pacificus and C. elegans to other nematodes, the authors convincingly argue that features observed in P. pacificus likely reflect an ancestral state. This depth greatly enhances the significance of the conclusions.

This work is likely to have a significant impact on the fields of comparative neurobiology and nervous system evolution. It demonstrates a powerful system and approach for linking molecular identity, cell-type homology, circuit context, and behavior across species. The data generated here will be a valuable resource for the community and provide a strong foundation for future mechanistic studies.

More broadly, the study reinforces the idea that evolutionary change in nervous systems can occur through modulation of chemical signaling within conserved circuits, rather than through complete rewiring. This conceptual framework is likely to influence how researchers think about neural evolution in other systems.

Weaknesses:

Given the availability of detailed connectivity information for both species, a more explicit comparison of the local circuit context of key neurons would further strengthen the link between molecular identity and circuit function.

We plan to address these concerns in a revised version of the article.

Reviewer #3 (Public review):

Summary:

The study by Hong, Loer, Hobert, and colleagues is a comprehensive description of monoaminergic neurons in the nematode Pristionchus pacificus. The work used multiple, complementary approaches, including immunostaining and expression of genes involved in neurotransmitter synthesis or transport, to identify neurons that express a monoamine neurotransmitter. Moreover, this study characterized the phenotypes of various mutants to study their organismal function. Extensive comparisons are made to C. elegans, the nematode model that, in a way, anchors the model studied here, and new outgroup species were examined for some features so that the polarity of their evolution could be inferred. Although there is no simple or groundbreaking punchline to distill from the manuscript (i.e., other than some things are the same as in C. elegans, and some things are different), and while the study is basically descriptive in nature, the scope of the project warrants broad attention.

Strengths:

This manuscript offers a tremendous resource for those who use this species as a model, which, based on the author list alone, includes many labs. This study sets the bar for what can be done in a "satellite" model system.

Given the complementarity of approaches used, such as the position of cell bodies, the connectivity and morphology of dendrites, and a previously published atlas of the connectome for this species, the identification of specific neurons (which, as the authors point out, can be easily mistaken) is convincing throughout. Likewise, appropriate caution is observed where neuron identities are ambiguous, e.g., unlabeled cells in Figure 5, or ambiguous identities in other species, as shown in Figure 10. There was a lot of data to unpack in this manuscript, but I could not find any obvious flaws in neuron identification.

Also, the phenotypic assays were straightforward and informative.

Weaknesses:

No serious weaknesses were noted. One minor comment is that in general, I think the Methods could use some additional text to describe what the goal of any given technique was. For example, although there is a description of the HCR protocol in the methods, nowhere does it say what genes this method would be used for. In addition to what is shown in Figure 4, this information should be given in the Methods.

More detailed methods will be provided in a revised version of the article.

Author response:

Public reviews:

Reviewer #1 (Public review):

(1) We agree that the current design does not allow us to cleanly dissociate whether the beneficial effect of retrieval practice on AC inference under stress reflects a selective enhancement of inferential processing or, instead, stronger memory for the underlying AB and BC premise pairs that supports later inference. We plan to revise the manuscript to remove wording that could be read as claiming that retrieval practice specifically protects inference independently of associative-memory strengthening.

Our intended interpretation is more modest. As shown in Section 3.2.3, retrieval practice improved direct premise-memory performance, consistent with the well-established testing effect. In the present paradigm, successful AC inference necessarily depends on access to the AB and BC premise associations. Accordingly, strengthened premise memory is not an alternative explanation that can be excluded by our data, but rather a plausible mechanism through which retrieval practice may promote more resilient inference performance under stress.

Because AC inference in our paradigm necessarily depends on retrieving and linking the AB and BC premise pairs, strengthened premise memory is not merely a competing explanation that can be separated from inference performance in the current dataset. Rather, it is a plausible mechanism through which retrieval practice may support inference, especially under stress. We therefore will revise the manuscript to avoid implying that retrieval practice protects inferential processing independently of associative-memory strengthening, and instead interpret the effect more conservatively as reflecting enhanced premise representations and/or more effective reactivation of bridge information during inference.

We also agree that the post-inference direct memory test, which used a 2AFC format, provides only a coarse measure of premise-memory strength and allows some proportion of correct responses to arise from guessing. Therefore, restricting analyses to trials in which AB and BC were later answered correctly does not fully guarantee that those trials were supported by strong associative memories. We will acknowledge this limitation explicitly in the manuscript and have tempered our interpretation of these “successfully retrieved” premise trials accordingly. More stringent measures, such as cued recall, confidence-based memory judgments, or other continuous indices of premise-memory strength, would be better suited to this question in future work.

Finally, we agree that the absence of a retrieval-practice benefit in the non-stress condition does not by itself rule out mediation through strengthened premise memory. Because the retrieval-practice manipulation was introduced in a follow-up study after completion of Study 1, the present dataset was not designed as a single fully crossed factorial experiment. In response to the reviewer’s suggestion, we will add an exploratory mediation analysis testing whether premise-memory performance statistically accounts for the relationship between retrieval practice and inference performance. We will report this analysis cautiously, given that premise memory was assessed using a post-inference 2AFC measure, and we note in the manuscript that a future fully crossed design with more sensitive premise-memory measures will be needed for a stronger test.

(2) We apologize that the presentation of Figure 4A was not sufficiently clear and may have created the impression of below-chance inference performance. The values shown in Figure 4A do not represent raw 3-alternative forced-choice (3AFC) A-C inference accuracy, for which the theoretical chance level would be 0.33. Instead, Figure 4A plots a normalized inference index, calculated as inference performance relative to direct retrieval performance, to account for individual differences in the availability of the directly learned premise pairs. Therefore, the raw 3AFC chance level is not the appropriate reference for interpreting this measure. To avoid this confusion, we will clarify in the revised manuscript and figure legend that Figure 4A shows a normalized inference index rather than raw inference accuracy.

(3) We agree that implementing retrieval practice in a separate experiment, rather than within a single 2 × 2 factorial design, limits the strength of the causal inference regarding retrieval practice and reduces our ability to formally test the retrieval practice × stress interaction within one unified design.

In response, we will revise the manuscript to more explicitly acknowledge this limitation and to temper our interpretation throughout. Specifically, we now avoid overstating retrieval practice as definitively preventing the effects of stress, and instead describe the findings more cautiously as evidence that retrieval practice was associated with attenuation of stress-related inference impairments across experiments. We also will add a limitation statement in the Discussion noting that the current design cannot fully rule out cohort-related confounds and that a fully crossed factorial design will be necessary in future work to provide a more rigorous test of the interaction between retrieval practice and stress.

At the same time, we have clarified that the two experiments were conducted under closely matched conditions: participants were recruited using the same protocol from the same campus population, demographic characteristics were matched, and both experiments were run in the same laboratory using the same EEG system, task procedures, and experimenter team. We agree, however, that these procedural consistencies reduce but do not eliminate the concern about between-experiment confounds.

(4) We agree that the absence of a matched re-exposure/restudy control condition limits the mechanistic interpretation of the retrieval-practice effect. In the revised manuscript, we will make this limitation more explicit in the Discussion and temper our conclusions accordingly. Specifically, we clarify that the present design shows that a post-encoding retrieval-practice intervention buffered the impact of acute stress on later inference, but it does not allow us to determine whether this benefit is specific to retrieval practice per se, rather than to additional exposure to the AB and BC associations.

We also agree that it is important to distinguish whether the effect operates at the level of specific practiced items or reflects a more global participant-level effect. In the current study, however, the retrieval-practice phase in Experiment 2 was implemented as a brief timed free-recall procedure rather than a trial-by-trial cued retrieval task, and the available records do not allow us to reliably link retrieval-practice success for individual associations to specific later AC inference trials. Therefore, we cannot directly compare later inference performance for successfully versus unsuccessfully retrieved items on a trial-by-trial basis.

To address this issue as far as possible with the current dataset, we instead plan to conduct an additional item-level robustness analysis using mixed-effects models that accounted for variability across ABC associations. Specifically, we tested whether the critical stress-by-retrieval-practice effect remained after modeling triad-level variability, and whether there was evidence that this effect differed substantially across triads. This analysis does not provide a direct test of whether successfully retrieved items benefit more than unsuccessfully retrieved items, but it does help assess whether the observed effect is broadly distributed across associations or driven by only a small subset of items.

(5) We agree that our current decoding approach does not justify a strong claim of item-specific reinstatement of a unique bridge memory. The classifier was trained to discriminate stimulus categories (faces vs. buildings) in the independent localizer and then applied during the inference phase. Therefore, the present analysis is better interpreted as indexing reactivation of bridge-related category information, rather than reinstatement of an item-specific episodic representation.

Importantly, however, we believe this signal remains theoretically informative for the inferential process examined here. In our design, the bridge element B belonged to one of the trained categories, and the classifier was applied during the cue period when no face or building stimulus was physically present. Thus, successful decoding in this time window suggests that task-relevant bridge-related information was re-expressed online during inference, rather than reflecting concurrent perceptual processing. At the same time, we agree that, because only two categories were used, the decoding analysis cannot fully dissociate bridge-related category reactivation from broader category-level retrieval, strategic task differences, or attentional contributions.

To address this concern, we plan to revise the manuscript in three ways. First, we will soften the interpretation throughout the Results and Discussion to avoid claims of item-specific bridge-memory reinstatement. Second, we now refer to the decoding effect more conservatively as bridge-related or category-level mnemonic reactivation during inference. Third, we have added an explicit limitation stating that the current design does not allow us to distinguish item-specific episodic reinstatement from category-level reactivation, and that future work using more fine-grained representational analyses and/or a larger stimulus set will be needed to resolve this issue more directly.

Reviewer #2 (Public review):

(1) We agree with this important point. The inference task was scheduled to begin approximately 20 minutes after stress onset based on prior human stress literature, with the intention of probing a time window commonly associated with glucocorticoid effects. However, as the reviewer notes, this period may also still reflect residual adrenergic/SAM influences. Because salivary cortisol was not collected due to the COVID-19-related safety protocol, we cannot disentangle the relative contributions of glucocorticoid and adrenergic responses to the observed stress-related effects on inference and neural reactivation. We will revise the manuscript to make this limitation more explicit in the Discussion and to avoid attributing the effects to a specific physiological component of the stress response.

(2) In the revised manuscript, we will add asterisks (or equivalent significance annotations) to Figures 4 and 6 to improve clarity and readability.

Reviewer #3 (Public review):

(1) We thank the reviewer for highlighting this important reporting issue. We agree that the number of trials contributing to the behavioral and EEG analyses should be reported more explicitly, particularly because inference performance was analyzed in relation to direct retrieval performance and because direct retrieval differed across experiments.

In the revised manuscript, we will report, for each group and experiment, the number of trials presented in the AC inference phase, the number of trials retained for the behavioral analyses, and the number of successfully retrieved direct-memory trials in the AB and BC tasks. These values will be summarized in the revised Results section and in Supplementary Tables.

To directly address the reviewer’s concern, we will also compared trial counts across groups/experiments and evaluated whether differences in direct retrieval performance could account for the inference and EEG effects. To further address the concern about potential unequal trial numbers, we plan to repeat the analyses such as trial-count-matched subsets analyses to see whether results remained qualitatively unchanged.

(2) We thank the reviewer for this important comment. We agree that our original title and some parts of the manuscript used language that was stronger than warranted by the data. Our results show that rapid reactivation of the bridge element is associated with successful inference and is modulated by stress and retrieval practice, but they do not by themselves establish a causal mechanistic role for reactivation. We therefore plan to revise the title and softened the relevant wording throughout the manuscript to better reflect the correlational nature of this evidence.

Specifically, we plan to change the title from “Retrieval practice prevents stress-induced inference impairment by restoring rapid memory reactivation” to “for example, Retrieval practice prevents stress-induced inference impairment and preserves rapid bridge-item memory reactivation” We also revised the Abstract, Results, and Discussion to replace stronger mechanistic wording such as “prevents,” “restoring,” and “essential neural mechanism” with more cautious phrasing such as “buffers” or “attenuates,” “preserves” or “is associated with,” and “neural correlate” or “candidate process,” as appropriate. This revision will led us to temper the overall interpretation of the EEG findings: rather than claiming that reactivation is the mechanism by which retrieval practice prevents stress-related inference deficits, we now conclude that rapid bridge-item reactivation is a neural correlate of successful inference that is sensitive to stress and enhanced by retrieval practice.

We also appreciate the reviewer’s concern regarding the use of one-tailed follow-up tests and the absence of multiple-comparison correction. With respect to the one-tailed t-tests, these follow-up comparisons were conducted because the relevant hypotheses were directional a priori. Based on prior work and our theoretical framework, we specifically predicted that acute stress would impair inference-related performance and neural reactivation, and that retrieval practice would mitigate these effects. The follow-up tests were therefore not exploratory post-hoc comparisons, but planned tests used to decompose the significant omnibus effects in the predicted direction. For this reason, we considered one-tailed testing appropriate for these comparisons.

Similarly, we did not apply an additional multiple-comparison correction to these planned follow-up tests because they were limited in number, theory-driven, and conducted to evaluate specific directional predictions rather than to search broadly across many possible contrasts. Importantly, our interpretation does not depend on any isolated post-hoc comparison, but on the consistency of the results across behavioral inference measures, neural decoding of bridge-item reactivation, and theta-band analyses. We have revised the manuscript to make this rationale clearer and to ensure that the follow-up results are interpreted in the context of the full pattern of evidence.

(3) We agree that, in the previous version, parts of the manuscript were not structured clearly enough, which may have made it difficult for readers to follow the logic of the study and the sequence of analyses without moving back and forth across sections. In the revised manuscript, we will reorganize the presentation to improve the overall narrative flow and readability. Specifically, we plan to clarify the study logic and analysis sequence, strengthened transitions between sections, and revised the relevant text in line with the #reviewer3’s detailed suggestions.

Author response:

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

We thank the reviewers and editors for their thoughtful comments, which substantially improved the quality and clarity of our manuscript. We have attempted to address each major concern with either new experiments or significant textual revisions.

Reviewer 1 noted that “this research is conducted exclusively in HEK293 cells… including at least one additional cell line would significantly strengthen the main findings.” To directly address this concern, we repeated our RAB1A/B double-knockdown experiments in H4 neuroglioma cells, which endogenously express a tandem fluorescent-tagged LC3B reporter. Using flow cytometry to quantify autophagic flux, we confirmed that RAB1 depletion in H4 cells recapitulates the flux defects observed in HEK293 cells, thereby validating the generality of our findings across distinct lineages.

To validate the robustness of the ATG2 DKO phenotype and the localization of ARFGAP1-positive membranes, we acquired an ATG2 double knockout HeLa cell line. We confirmed the presence of the characteristic large ATG2-deficient PAS compartment in HeLa cells, and the recruitment of ARFGAP1 membranes, but note that ARFGAP1 displays a solid distribution through the compartment in these cells, in contrast to the more peripheral enrichment observed in HEK293 cells. These data are now included and discussed in the revised manuscript.

Multiple reviewers asked for greater clarity around the interaction between ATG2A and RAB1A. Although our original data showed that these proteins co-immunoprecipitate in cells, we had not established whether their association was direct. In response, we attempted in vitro co-immunoprecipitations from purified components.  As we could not detect interactions in this simplified system, we now speculate that the ATG2A–RAB1A interaction is indirect. This clarification is now incorporated into the results section.

Multiple reviewers also raised questions regarding the nature of the membranes recruiting ARFGAP1 and the potential relationship to Arf1 and Golgi trafficking. In particular, Reviewer 3 asked: “(5) What about Arf1? … one would predict that Arf1 does not localize to these structures and does not affect ATG2A function.” To examine whether ARFGAP1 recruitment depends on Golgi integrity or Arf1-regulated trafficking, we perturbed the Golgi using three mechanistically distinct methods: Brefeldin A, mitotic entry, and SidM expression, each of which dissolves Golgi architecture. In each condition, ARFGAP1 localization to the enlarged PAS compartment in ATG2 DKO cells was unchanged. These results indicate that ARFGAP1 recruitment is independent of Golgi structure and provide indirect support for the notion that Arf1 does not participate in this process. Reviewer 3 also asked: “Is the curvature-sensitive region of ARFGAP1 required for its co-localization with ATG2A?” To address this, we generated ARFGAP1 mutants lacking either GAP catalytic activity or the ALPS curvature-sensing domain. When expressed in ATG2 DKO cells, all mutants retained full recruitment to the PAS compartment. Thus, neither GAP activity nor ALPS-mediated curvature sensing is required for ARFGAP1 localization in this context.

Response to Reviewer 3 -“(2) Figure 3A/B: … is there another tool/assay to validate this result?”—we quantified autophagic flux following SAR1B(H79G) overexpression using the flow-cytometry tandem-fluorescent LC3 assay. These experiments confirmed that SAR1B(H79G) causes only a modest reduction in autophagic flux, consistent with partial inhibition of COPII, thereby supporting our original interpretation.

We also took steps to improve the integration of our findings with prior literature. Reviewer 2 requested that we strengthen the manuscript by incorporating studies on ERES–ERGIC remodeling (“It would strengthen the manuscript to discuss previous studies…”). We now cite and discuss the studies corresponding to PMIDs 34561617 and 28754694, aligning our observations with mechanistic models of early secretory pathway remodeling. More broadly, Reviewer 1 commented that our discussion “overlooks some important aspects,” and Reviewer 3 asked, “Are the membranes to which ATG2A is recruited a form of ERGIC?” In response, we substantially rewrote the discussion, expanding our integration of existing literature and explicitly addressing models in which ATG2A acts at an ERGIC-derived membrane.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

(1) I found the bigger picture analysis to be lacking. Let us take stock: in other work, during active cognition, including at least one study from the Authors, TDLM shows significance sequenceness. But the evidence provided here suggests that even very strong localizer patterns injected into the data cannot be detected as replay except at implausible speeds. How can both of these things be true? Assuming these analyses are cogent, do these findings not imply something more destructive about all studies that found positive results with TDLM?

Our focus here is on advancing methodology. Given the diversity of tasks and cognitive states in the TDLM literature, replay could exceed detection thresholds under specific conditions—especially when true event durations align with short analysis windows. While a comprehensive re-analysis of prior datasets is beyond our scope, we agree a concise synthesis can strengthen the paper.

The previous TDLM literature uses a diverse set of tasks and addresses a broad spectrum of cognitive constructs/processes. As we acknowledge, it is perfectly possible that replay bursts in short time windows are well detectable by TDLM. However, we acknowledge that some commentary on this is warranted and have added the following paragraph to the discussion that addresses “improving TDLMs sensitivity”:

“Finally, what do our simulations imply for the broader MEG replay literature? Our implementation successfully detects replay when boundary conditions are met, as shown in the simulation. But sensitivity depends critically on high fidelity between the analysis window and the density of replay events. A systematic evaluation of these conditions as they apply to prior studies remains beyond the scope of the current paper. Instead, our focus is on delineating boundary conditions that we hope will motivate conduct of power analyses in future work as well as inclusion of simulations that approximate realistic experimental conditions.”

(2) All things considered, TDLM seems like a fairly 'vanilla' and low-assumption algorithm for finding event sequences. It is hard to see intuitively what the breaking factor might be; why do the authors think ground truth patterns cannot be detected by this GLM-based framework at reasonable densities?

We agree with the overall sentiment of the referee. Our intuition is that one of the principal shortcomings of the method relates to spurious sequenceness induced by unknown factors at baseline, and poor transfer of the decoder to other modalities. and have a rough understanding of how they occur, we are currently not in a position to identify their nature. Note that we believe that these confounders are not exclusive to TDLM but are potentially threatening to all kinds of sequenceness analysis of longer time series that rely on decoders. Indeed, we suspect that classifier training is another bottleneck, as we don’t know the exact nature of the representations that are replayed, including the degree of overlap there is with a commonly used visual localizer. That said, this is not of relevance for the simulation in so far as we insert patterns that exceed the pattern strength in the localizer.

Finally, a potential major drawback is the permutation test for significance testing. As the original authors of TDLM have noted, the current test which permutes states is overly conservative. It measures fixed effects and as it only considers the group level mean it is accordingly easily biased by individual outliers. This we have tried to account for by z-scoring sequenceness scores. We have also conferred on this with some of the authors of TDLM and discussed a yet unpublished method that aims to address this exact issue. The proposed new method uses a sign-flip permutation test at a group level and therefore implements a random-effects model of the data. This significance test has markedly increased power while still controlling for FWER. However, while we show in our power analysis that the new method is indeed more sensitive, it does not materially change the interpretation of the data. We have included this novel method in the paper and added it into the main analysis and most of the simulations.

(3) Can the authors sketch any directions for alternative methods? It seems we need an algorithm that outperforms TDLM, but not many clues or speculations are given as to what that might look like. Relatedly, no technical or "internal" critique is provided. What is it about TDLM that causes it to be so weak?

We believe there are several shortcomings and bottlenecks within TDLM that need to be evaluated and improved. While we highlight these issues in the discussion section titled “Improving TDLMs sensitivity,” we agree that we should provide a clearer outline of its current shortcomings. We have now added to the discussion to expand on that we think needs improvement (‘fixed time lag’) and also add a summary statement at the end of the relevant paragraph to recap the main issues needed for an improved successor method. The new paragraphs read:

“Lastly, there are certain assumptions that TDLM makes that might not hold (see Methods Study II): Current implementations look for a fixed time lag that is the same across all participants and between all reactivation events. If time lags differ across participants, TDLM will fail to find them. Similarly, TDLM assumes a fixed sequence order and is not robust against slight within-sequence permutations or in-sequencemissing reactivation events. However, from other data sources., such as hippocampal place cell recordings, it is known that such permutations can occur where some states are skipped or fail to decode during replay. Similarly, it is assumed that each reactivation event lasts between 10-30 milliseconds, but the true temporal evolution of reactivation measured by TDLM is currently unknown. Future method development might focus on improving invariance to these assumptions.

[…]

In summary, there are several areas where TDLM might be improved, including a restriction in its search space, improvement in classifiers, a validation of localizer representation transfer to other domains (e.g. memory representations), and the extension of TDLM to render it more robust against violations of its core assumptions.”

Reviewer #2 (Public review):

Weaknesses:

The sample size is small (n=21, after exclusions), even for TDLM studies (which typically have somewhere between 25-40 participants). The authors address this somewhat through a power analysis of the relationship between replay and behavioural performance in their simulations, but this is very dependent on the assumptions of the simulation. Further, according to their own power analysis, the replay-behaviour correlations are seriously underpowered (~10% power according to Figure 7C), and so if this is to be taken at face value, their own null findings on this point (Figure 3C) could therefore just reflect under sampling as opposed to methodological failure. I think this point needs to be made more clearly earlier in the manuscript.

We agree with the referee that our sample is smaller than previous studies due to participant exclusion criteria. However, the take-away message from our behavioural simulation and bootstrapping is that even with larger sample sizes, it is difficult to overcome baseline fluctuations of sequenceness, even if very strong replay patterns were detectable and sample sizes were of similar size to that of previous studies. Therefore, we are not convinced that that our null findings are fully explained by the smaller sample size compared to that of previous studies, Additionally, we show that even within the range of other studies, similar power would have been expected (Supplement Figure 11). However, it is true that in general null findings can be explained by under-sampling, under the assumption that an effect is present. To amplify this point, we have added the following to the Figure 3C:

“[…]. NB, however, as our simulation shows, correlations of sequenceness with behavioural markers are likely to be underpowered and occur only with very high replay rates or much higher sample size. See our simulation discussion for a more detailed explanation on how correlations may be inherently biased, where fluctuations in baseline sequenceness overshadow individual scaling with behavioural markers.”

Furthermore, we have added the following paragraph to the discussion to highlight this point and refer to a power analysis we have now added to the supplement (see next answer):

“Sample sizes in previous TDLM literature usually range between 20 to 40 participants. A bootstrap power analysis shows that even at those sample sizes, power would remain low unless unrealistically high replay rates are assumed (Supplement Figure 11). Our bootstrap simulation shows that a correlation analysis between sequenceness and behaviour would in these cases be drastically underpowered, even under an assumption of high replay densities.”

Finally, we have added a remark about the sample size to the limitations section, as naturally, an increase in sample size would yield higher power:

“Finally, while initially planning for thirty participants, due to exclusion criteria, our study featured fewer participants than most previous studies using TDLM (i.e. usually 25-40, but 21 in our study). While we are confident that our simulation results hold under these sample sizes, as sample sizes of other studies show comparable power to ours (Fehler! Verweisquelle konnte nicht gefunden werden.), we cannot fully rule out a possibility that our null-findings are explained by a lack in power alone.”

Relatedly, it would be very useful if one of the recommendations that come out of the simulations in this paper was a power analysis for detecting sequenceness in general, as I suspect that the small sample size impacts this as well, given that sequenceness effects reported in other work are often small with larger sample sizes. Further, I believe that the authors' simulations of basic sequenceness effects would themselves still suffer from having a small number of subjects, thereby impacting statistical power. Perhaps the authors can perform a similar sort of bootstrapping analysis as they perform for the correlation between replay and performance, but over sequenceness itself?

We agree with the referee that this, in principle, is a great idea. However, the way that significance thresholds are calculated poses a conceptual problem for such an analysis: as for significance threshold we are defining the maximum sequenceness value across all participants, all time lags and all permutations. This sequenceness value is compared against the mean of all participants, disregarding the standard deviation. This maximum threshold would not change if we bootstrapped some of our samples. Additionally, the 95% would also not change significantly. To illustrate this point, we have added this analysis to the supplement, as Supplement Figure 10. However, the new sign-flip permutation test we now include allows for such a comparison, as it takes variance between participants into account as well! We have included all three variants of the power analysis and the figure description now reads:

“Supplement Figure 11 Power analysis of sequenceness significance for bootstrapped samples sizes. A) Powermap for state-permutation thresholds. However, here the bootstrap approach suffers from a conceptual problem: significance thresholds are defined by the permutation maximum and/or 95-percentile of the maximums across all sequence-permutations across participants. If we resample bootstrap-participants from our existing pool, the maximum thresholds computed will remain relatively stable across resampled participants, as it only compares against the mean and disregards the standard deviation. B) The newly presented statistical approach is significantly more sensitive at higher sample sizes. Note that even then, 80% power is only reached with replay density of higher than 50 min-1 at a sample size of 60 participants. Additionally, the sign-flip permutation test assumes that the mean is at zero. As we observed a non-zero mean due to spurious oscillations, we subtracted the mean sequenceness of the baseline condition from each participant before permuting to achieve a null distribution with mean zero, as otherwise, we would have found significant replay effects in the baseline condition at increasing sample size. Nevertheless, due to the higher sensitivity, the new sign-flip test is recommended over the previous sequence-permutation-based test. Colours indicate the power from 0 to 1 for different bootstrapped sample sizes and densities. 80% power thresholds are outlined in black.”

The task paradigm may introduce issues in detecting replay that are separate from TDLM. First, the localizer task involves a match/mismatch judgment and a button press during the stimulus presentation, which could add noise to classifier training separate from the semantic/visual processing of the stimulus. This localizer is similar to others that have been used in TDLM studies, but notably in other studies (e.g., Liu, Mattar et al., 2021), the stimulus is presented prior to the match/mismatch judgment. A discussion of variations in different localizers and what seems to work best for decoding would be useful to include in the recommendations section of the discussion.

We agree and thank the referee for raising this issue. Note, we acknowledge we forgot to mention that these trials were excluded from classifier training. Our rationale of presenting the oddball during stimulus presentation, and not thereafter, was an assumption that by first presenting the audio and then the visual cue we would create more generalized representations that would be less modalitydependent. However, importantly, we excluded all trials that were oddballs from localizer training. Therefore we assume that this particular design choice will not greatly affect the decoder training. If some motor-preparation activity is present during the stimulus presentation, then it should be present equally across all trials and hence be ignored by the classifier as we balanced the transitions between images. We now added this information to the main text:

“In each trial, a word describing the stimulus was played auditorily, after which the corresponding stimulus was shown. In ~11% of cases, there was a mismatch between word and image (oddball trials), and these trials were excluded from the localizer training.” Additionally in the methods section: “These oddball-trials were excluded from all further analysis and decoder training.”

Nevertheless, we agree that the extant variety in localizer designs is underdiscussed where many assumptions of classifier training are not, as yet, fully validated. We have added a sentence highlighting different oddball paradigms to the section on the discussion of localizers and also add a summary statement with recommendations. The passage now reads:

“Additionally, a wide variety of oddballs has been used (e.g. upside-down, scrambled, or mismatched images, cues presented visually, as words, auditorily, etc), and at this time it is unclear if these affect the representations that the classifier learns [...] In summary, we would expect a multimodal categorical localizer, and a classifier that isn’t trained on a specific timepoint, to generalize best.”

Second, and more seriously, I believe that the task design for training participants about the expected sequences may complicate sequence decoding. Specifically, this is because two images (a "tuple") are shown together and used for prediction, which may encourage participants to develop a single bound representation of the tuple that then predicts a third image (AB -> C rather than A -> B, B -> C). This would obviously make it difficult to i) use a classifier trained on individual images to detect sequences and ii) find evidence for the intended transition matrix using TDLM. Can the authors rule out this possibility?

We thank the reviewer for raising a possibility we have not considered! While there is some evidence that a single bound representation would have overlap with its constituents (especially before long term-consolidation) and therefore be detectable by the classifiers, we acknowledge the possibility that individual classifiers would fail to be sensitive to such a compound representation. In fact we find in the retrieval data some evidence for a combined replay of representations (where representations are replayed seemingly at the same time, see Kern 2024). We have added such a possibility to the interims-discussion of Study 1 as a qualification . However, this does not change the results or interpretation of our simulation which we consider is a key message of the paper.

The relevant segment in the discussion section now reads:

“Additionally, given that the stimuli were presented in combined triplets, participants may have formed a singular representation of associated items and subsequently replayed these (e.g., AB→C), instead of replaying item-by-item transitions (A→B→C). Under such a scenario, a classifier trained on individual items may fail to detect these newly formed bound representations, particularly if they diverge strongly from the single-item patterns. In our previous study where we address retrieval (Kern et al., 2024) we found that states were to varying extent co-reactivated, yet classifiers trained on single items retained sensitivity to detect these combined reactivation events. Consistent with this, prior work suggests that unified representations retain overlap with their constituent item representations (Dennis et al., 2024; Liang et al., 2020), however, there’s also evidence that different brain regions are involved if representational unitization occurs (Staresina & Davachi, 2010), potentially confusing classifiers. Therefore, we cannot exclude that rest-related consolidation replays engendered unitized representations that were insufficiently captured by our singleitem classifiers.“

Participants only modestly improved (from 76-82% accuracy) following the rest period (which the authors refer to as a consolidation period). If the authors assume that replay leads to improved performance, then this suggests there is little reason to see much taskrelated replay during rest in the first place. This limitation is touched on (lines 228-229), but I think it makes the lack of replay finding here less surprising. However, note that in the supplement, it is shown that the amount of forward sequenceness is marginally related to the performance difference between the last block of training and retrieval, and this is the effect I would probably predict would be most likely to appear. Obviously, my sample size concerns still hold, and this is not a significant effect based on the null hypothesis testing framework the authors employ, but I think this set of results should at least be reported in the main text.

We disagree that an absence or presence of replay might be inferred from an absolute memory enhancement. While consolidation can lead to absolute improvement of performance in, for example, motor memory domains one formulation is that in declarative learning tasks replay stabilizes latent memory traces, and in such a scenario would not necessarily lead to a boosted performance. While many declarative consolidation studies report an increase of performance compared to a control condition (i.e. without a consolidation window), this does not necessarily entail an absolute performance increase, as replay might just act to protect against loss of memory traces. Therefore, the modest increase we observe does not inference as to the presence of absence of replay absent a proper control condition.

We did expect to find a correlation between replay and individual behavioural. Indeed, a weak correlation with performance and sequenceness can be detected. However, as we also show any such correlation is overshadowed by baseline fluctuations in sequenceness such that its overall validity is questionable, even under very high replay rates. We are therefore circumspect about this correlation, even if it was significant. Therefore, in the discussion, we chose to refrain from putting much focus on this correlation. Nevertheless, we do add a short statement to the corresponding figure label, discussing this precise issue. The segment now reads:

“While we found a non-significant relation between a memory performance enhancement and post-learning forward sequenceness we are cautious not to overinterpret these results. As in the section “Correlation with behaviour only present at high replay speeds” the noted correlational measure oscillates heavily with baseline sequenceness fluctuations, and any true replay effect is likely to be overshadowed by such fluctuations.”

I was also wondering whether the authors could clarify how the criterion over six blocks was 80% but then the performance baseline they use from the last block is 76%? Is it just that participants must reach 80% within the six blocks *at some point* during training, but that they could dip below that again later?

We thank the reviewer for highlighting this point: The first block wherein participants reached >80% ended the learning blocks. After a maximum of six blocks the learning session was ended regardless of performance. Therefore, some participants’ learning blocks were ended after six blocks and without them reaching a performance of 80%.. While we described this in the Methods section, it was missing from the Results Study I section, which now contains:

“[...] Participants then learned triplets of associated items according to a graph structure. Within the learning session, participants performed a maximum of six learning blocks, but the session was stopped if participants reached 80% memory performance (criterion learning,, up to a memory performance criterion of 80% (see Methods for details)”

The Figure 2 description now contains

“[...] Participants’ completed up to six blocks of learning trials. After reaching 80% in any block, no more learning blocks were performed (criterion learning) [...]”

Lastly, there was a mistake in the Behavioural results section, which stated “All thirty participants, except one, [..] to criterion of 80%.” This is an error. In our preregistration, we defined to only include participants that successfully learned anything at all above chance. Here,we meant that only one participant failed to reach a criterion that we defined as “successful learning”. We fixed it and it now reads

“with an accuracy above 50% (which we preregistered beforehand as an exclusion criterion for “successful learning above chance”).”

Additionally, we have noted this for clarity in the methods section and excuse this mistake:

“Additionally, as successful above-chance learning was necessary for the paradigm, we ensured all remaining participants had a retrieval performance of at least 50% (one participant had to be excluded, but was already excluded due to low decoding performance).”

Because most of the conclusions come from the simulation study, there are a few decisions about the simulations that I would like the authors to expand upon before I can fully support their interpretations. First, the authors use a state-to-state lag of 80ms and do not appear to vary this throughout the simulations - can the authors provide context for this choice? Does varying this lag matter at all for the results (i.e., does the noise structure of the data interact with this lag in any way?)

This was a deliberate choice but we acknowledge the reasoning behind this was not detailed in our initial submission. We chose a lag of 80 millisecond for three reasons: first, it is distant from the 9-11 Hz alpha oscillations we observed in our participants and does not share a harmonic with the alpha rhythm; second, we wanted to get a clear picture of the effect of simulated replay that is as isolated as possible from spurious sequenceness confounders present in the baseline condition. Thus, we chose a lag in which the sequenceness score was close to zero in the baseline condition; thirdly , in this revision, we subtracted the mean sequenceness value of the baseline such that any simulation effects would start, on average, at zero sequenceness. In this way, we could attribute any increase in sequenceness to the experimentally inserted replay, that was independent of spurious oscillations. Finally (but less importantly), as we observed that a correlation of sequenceness with behaviour was fluctuated strongly, for the reason detailed above, we chose a lag in which a correlation was as close as possible to zero. If we had not chosen a lag that adhered to these conditions, we were at risk of measuring simulated replay plus spurious sequenceness confounders.

We have added a sentence to the main text detailing this justification:

“We chose this timepoint (80 msec state to state lag) as its sequenceness value was close to zero in the baseline condition as well as being distant to the observed alpha rhythms of the participants (which varied between ~9-11 Hz). Additionally, we subtracted the mean sequenceness value of the baseline at 80 milliseconds lag such that any simulation effects would, on average, start at zero sequenceness “

Additionally, we now add a more detailed explanation to the methods section.

“This time lag (80 msec) was chosen in order to isolate precisely an effect of the experimentally inserted sequenceness. Thus, we chose a lag at which the mean baseline sequenceness was close to zero and where the correlation with behaviour was low. Additionally, we subtracted the mean sequenceness value (at 80 milliseconds) at baseline from the specific lag recorded for each participant, such that simulation effects would be initialized at zero sequenceness on average enabling any effects to be attributed purely to inserted replay. Additionally, we excluded time lags too close to the alpha rhythms of participants (which varied between ~9-11 Hz) or lags which would have a harmonic with the rhythm.”

Second, it seems that the approach to scaling simulated replays with performance is rather coarse. I think a more sensitive measure would be to scale sequence replays based on the participants' responses to *that* specific sequence rather than altering the frequency of all replays by overall memory performance. I think this would help to deliver on the authors' goal of simulating an "increase of replay for less stable memories" (line 246).

The referee makes an excellent point and our simulations could be rendered more realistic by inserting the actual tuples that participants answered correctly. If we understand the point correctly, there are two different ways replay might be impacted by performance: First, we can conjecture that there is greater replay if memory performance is not saturated. Second, replay only occurs for content that has actually been encoded!

The main reasons why we chose to simulate the entire sequence being replayed for each participant is based on the following. TDLM is implemented such that the amount of replay alone is relevant, and actual transitions are not affecting the results beyond noise. Under the assumption that class-specific classifiers perform equally well, simulating A->B, B->C or simulating A->B, A->B yields equivalent results. However, results can differ if this assumption is violated. By drawing from the entire space of classes we insert, we minimize the risk of some classifiers being worse than others for some participants. For example, if we simulated only A->B for some participant instead of the whole sequence, and by chance classifier A performs suboptimally, we would then introduce additional unwanted variance into our results.

Secondly, from our reading of the literature we infer that replay is increased generally (i.e. density of learning-specific replay is increased) for less stable memories. However, we do not have indicators of memory strength, but only a binary “remembered or not”. As TDLM is invariant to the actual transitions being replayed and only indexes the number of transitions, we chose to ignore which transitions we insert and only scaled the amount of replay.

We have added an analysis to the Appendix that discusses this specific aspect of our study where we show that results are equivalent if we simulate replay of “A->B B->C C->D” or only “A->B A->B A->B A->B”. As we do not know how replay density interacts with memory trace stability, we opted to leave the current simulation as is. The corresponding paragraph and figure description now read:

“From literature we know that replay is increased after learning and that less stable memories are replayed more often. We simulated this effect by scaling our replay density inversely with performance. However, for simplicity, in our simulation, we inserted sampled transitions from all valid transitions given by the graph structure, i.e., the following transitions were valid: However, this meant that some participants would have transitions inserted that they didn’t actually remember. To show that this would not change results, we simulated two scenarios: In the full sequence scenario, all valid graph transitions are inserted (i.e. all participant’s replay is sampled from 'A->B, B->C, C->D, D->E, E->F, F->G, G->E, E->H, H->I, I->B, B->J, J->A'). In the second scenario (memorized transitions) we only replayed transitions that the participant actually retrieved correctly during the post-resting state testing sessions (i.e. a participant’s replay would have been sampled from ‘A->B, B->C, G->E, E->H, H>I’, if those were the ones he remembered). In both scenarios, the number of events is kept constant. The results are equivalent as can be seen in Appendix A Figure 3. NB this only holds under the assumptions that classifiers are equally good at decoding each class.”

[…]

“TDLM is insensitive towards which transitions are replayed and only sensitive to how many transitions are detected in total. Here we simulate transitions either sampled from the full graph (light orange/green) or participant-specific transitions of trials that participants correctly remembered (dark orange/green). Shaded areas denote the standard error across participants.”

On the other hand, I was also wondering whether it is actually necessary to use the real memory performance for each participant in these simulations - couldn't similar goals (with a better/more full sampling of the space of performance) be achieved with simulated memory performance as well, taking only the MEG data from the participant?

The decision to use real memory performance is indeed arbitrary. We could have also used randomly sampled values. However, as we wanted to understand our nullresults better we opted to use real performance to adhere as close as possible to the findings we previously reported. Using uniformly sampled memory performance would be less explanatory w.r.t to our actual results of the resting state data that are reported in the first study we report in the manuscript (Study I).

Nevertheless, our current implementation already presents an approach that samples the entire performance range for the sub-analysis focusing on the correlation with behaviour. Here, in the section on “best-case”-scenario, we implement this such that it spans factors from 1 to 0 (i.e., a participant with 100% performance gets a replay scale factor of 0 and hence no replay simulated, and the worst performing participant with 50% performance has a replay rate multiplied by 1). We scale the amount of replay with this factor. As a correlation is invariant to linear scaling, statistically this is equivalent to stretching the performance distribution from 0 to 100%. We have added a sentence to the methods to provide further focus on this point:

“To assess how performance might affect replay in our specific dataset, we chose to use the original participants’ performance values instead of uniformly sampling the performance space (which ranged from 50 to 100%). However, for the correlation analysis, we additionally added a “best-case” scenario, in which we scale replay from 0 to 1, an approach that is statistically equivalent to scaling values to the full space of possible performance (0 to 100%) (see Results Study II: Simulation).”

Finally, Figure 7D shows that 70ms was used on the y-axis. Why was this the case, or is this a typo?

Thanks, this is indeed a typo, we fixed it.

Because this is a re-analysis of a previous dataset combined with a new simulation study on that data aimed at making recommendations about how to best employ TDLM, I think the usefulness of the paper to the field could be improved in a few places. Specifically, in the discussion/recommendation section, the authors state that "yet unknown confounders" (line 295) lead to non-random fluctuations in the simulated correlations between replay detection and performance at different time lags. Because it is a particularly strong claim that there is the potential to detect sequenceness in the baseline condition where there are no ground-truth sequences, the manuscript could benefit from a more thorough exploration of the cause(s) of this bias in addition to the speculation provided in the current version.

We are currently working on a theoretical basis to explain these spurious sequenceness confounders in the baseline condition. Indeed, in our preliminary work, in certain contexts we can induce significant sequenceness in the absence of any replay signal during baseline. However, this work is at an early stage and we still have some conceptional problems to solve before we are confident enough with these data. We believe at present it would be premature to add these data to the current manuscript. Nevertheless, we now mention these spurious sequenceness confounders to raise awareness for the field and also add greater context to the discussion, highlighting one of the issues that we think is of importance:

“[…] For example, if two classifiers’ probabilities oscillate at 10 Hz but at a different phase, a spurious time lag can be found reflecting this phase shift. We speculate that more complex interactions between classifiers oscillating at different phases are also conceivable.”

In addition, to really provide that a realistic simulation is necessary (one of the primary conclusions of the paper), it would be useful to provide a comparison to a fully synthetic simulation performed on this exact task and transition structure (in addition to the recreation of the original simulation code from the TDLM methods paper).

Thank you for this suggestion! We have now added a synthetic simulation, trying to keep as close as possible to the original simulation code in Liu et al. (2021), while also incorporating our current means of simulating the data (i.e. scaling by performance). We think this synthetic simulation greatly improves the paper and gives weight to our suggestion about the superiority of a hybrid approach. Additionally, it prompted us to look closer at patterns that are inserted in the synthetic simulation and perform a comparative analysis. We have now added the simulation to the main text, together with a methodological explanation of how we simulated the data in the methods section. We also added a discussion on the results and why we think a hybrid approach is currently superior to synthetic approach. The whole new section is too long to paste here – it is found after the main simulation section in the manuscript. We have also added another sentence to the abstract referring to this new inclusion.

Finally, I think the authors could do further work to determine whether some of their recommendations for improving the sensitivity of TDLM pan out in the current data - for example, they could report focusing not just on the peak decoding timepoint but incorporating other moments into classifier training.

While we do understand the desire to test further refinement to TDLM on the data directly, we intentionally do not include such analyses in the current paper. Our experience also informs us that there is an enormous branching factor of parameters when applying TDLM, with implications for significance of results in one or other direction. However, as there are currently only limited ways to know how well parameter changes actually improve the sensitivity to replay versus exacerbate potential underlying confounders that induce spurious sequenceness (e.g., we can get significant replay in the control condition with some parameter changes). To exclude such false positive findings, we opt for a relatively strict adherence to previously published approaches. Thus, in the current paper, we limit ourselves to assessing the reliability and robustness of previous approaches.

Furthermore, while training on a later timepoint might increase sensitivity for a classifier when transferring between different modalities (e.g. visual to memory representation), this approach does not transfer well in our simulations, as the inserted patterns are from the same modality. We consider other, more bespoke studies, are better suited to improve classifier training. NB also see our recently started Kaggle challenge to tackle this problem: https://www.kaggle.com/competitions/the-imagine-decoding-challenge

However, we have added a note about this dilemma to the improvement section. The section now includes:

“Nevertheless, as the considerable branching factor poses a threat of increased falsepositive findings we opt to focus the current simulations on previously published pipelines and parameters. Future studies should systematically evaluate parameter choices on TDLM under different conditions, something that is beyond the remit of the current study.”

Lastly, I would like the authors to address a point that was raised in a separate public forum by an author of the TDLM method, which is that when replays "happen during rest, they are not uniform or close." Because the simulations in this work assume regularly occurring replay events, I agree that this is an important limitation that should be incorporated into alternative simulations to ensure the lack of findings is not because of this assumption.

The temporal distribution of replay throughout the resting state should not matter, as TDLM is invariant w.r.t to how replay events are distributed within the analysis window. Specifically, it does not matter if replay events occur in bursts or are uniformly distributed. Only the number of transitions is relevant, where they occur or if they are close to each other is not relevant to the numerical results (as long as the refractory window is kept, too short distances will lead to interactions between events and reduce sensitivity).). To emphasize this point, we have added another simulation which is shown in Appendix A.1 and Appendix A Figure 1. We have referenced it in the text and added the following paragraph in the Methods section

Additionally, the timepoints of inserting replay within the resting state are sampled from a uniform distribution. Even though TDLM tracks reactivation events over time, at a macro-scale the algorithm is invariant to the temporal distribution. At each time step, the GLM regresses onto a future time step up to the maximum time lag of interest, yielding a predictor per lag. However, these predictors within the GLM are independently assessed, and hence, TDLM is, outside of the time lag window, relatively invariant to the temporal distribution of replay. To demonstrate our claim, we simulated uniform replay vs “bursty” replay that only occurs in some parts of the resting state, both yield equivalent sequenceness results (see Appendix A.1).

Reviewer #3 (Public review):

(1) I am still left wondering why other studies were able to detect replay using this method. My takeaway from this paper is that large time windows lead to high significance thresholds/required replay density, making it extremely challenging to detect replay at physiological levels during resting periods. While it is true that some previous studies applying TDLM used smaller time windows (e.g., Kern's previous paper detected replay in 1500ms windows), others, including Liu et al. (2019), successfully detected replay during a 5-minute resting period. Why do the authors believe others have nevertheless been able to detect replay during multi-minute time windows?

(Due to similarity, we combined our responses with the first question of Reviewer 1)

We are reluctant to make sweeping judgments in relation to previous literature as we wanted to prioritize on advancing methodology instead. The previous TDLM literature uses a diverse set of tasks and cognitive processes. As we state ourselves, it is possible that replay bursts in short time windows are well detectable by TDLM. We were intentionally cautious to directly critique previous studies without detailed re-analysis of their work and wanted to leave such a conclusion up to the reader. However, we realize that such a “thought-starter” might be warranted and improve the paper. Therefore, we have added the following paragraph to the discussion about “improving TDLMs sensitivity”:

“Finally, what do our simulations imply for the broader MEG replay literature? Our implementation successfully detects replay when boundary conditions are met, as shown in the simulation. But sensitivity depends critically on high fidelity between the analysis window and the amount of replay events. A systematic evaluation of these conditions across prior studies is beyond the scope of this paper, so we do not want to adjudicate earlier findings and leave this assessment up to the reader. Instead, we delineate the boundary conditions and urge future work to conduct power analyses where possible and include simulations that approximate realistic experimental conditions.”

For example, some studies using TDLM report evidence of sequenceness as a contrast between evidence of forwards (f) versus backwards (b) sequenceness; sequenceness was defined as ZfΔt - ZbΔt (where Z refers to the sequence alignment coefficient for a transition matrix at a specific time lag). This use case is not discussed in the present paper, despite its prevalence in the literature. If the same logic were applied to the data in this study, would significant sequenceness have been uncovered? Whether it would or not, I believe this point is important for understanding methodological differences between this paper and others.

This approach was first introduced as part of a TDLM-predecessor that utilized crosscorrelations (Kurth-Nelson 2016), where this step is a necessity to extract any sequenceness signal at all by subtracting signals that are present in both (akin to an EEG reference). However, its validity is less clear when fwd and bkw are estimated separately, as is in the GLM case. The rationale behind subtracting here is the same as for autocorrelations: there are oscillatory confounds present in the data that introduce spurious sequenceness in both directions alike, i.e. at the same time lag, that can simply be removed by subtracting. However, this assumption only holds if the sole confounder is auto-correlations caused by a global signal that oscillates at all sensors at the same phase. In our own experience, and mentioned in the discussion, we do not think this assumption holds. Arguably, there are more complex interactions at play that cannot be removed by such a subtraction such as an increase in false positives if confounders are in an opposite direction at a specific time lag. This assumption-violation can be seen in our baseline condition, where other spurious sequenceness diverges in opposite directions for some time lags (e.g. at ~90 ms where forward sequenceness is negative and backward sequenceness is positive). We reasoned that oscillatory confounds are more stable when comparing pre vs post for the same direction than comparing within session between forward minus backward.

Finally, we note issues introduced by the various ways that sequenceness has been analysed in previous papers: normalization of sequenceness (z-scoring across time lags or across participants or not at all), normalization of probabilities (taking raw decision scores, z-scoring, soft-max, dividing by mean, subtracting mean), taking a windowed approach and summing sequenceness scores, not to mention the various classifier choices that can be made, and all of this can be applied before subtracting conditions from each other or before subtraction. In our experience there is insufficient regard to control for multiple comparison when running all these analyses risking selectivity in reporting.

Nevertheless, subtracting forward from backward replay is probably as valid as post minus pre. Therefore, we have added fwd-bkw plots to the supplement and explained some of the reasoning for not reporting them in the main text in the figure label. The figure label and reference now read:

“Finally, we report forward minus backward sequenceness and our motivation for using an across-session post-pre comparison instead of within-session forwardbackward in Supplement Figure 10.”

[…]

“Forward minus backward sequenceness within each resting state session. Previous papers often report subtraction of backward from forward sequenceness (fwd-bkw) as a means to remove oscillatory confounds that impact both sequenceness directions in synchrony. While required in early cross-correlation approaches (KurthNelson et al., 2016), its validity in GLM-based frameworks depends on an assumption that confounds are global and in-phase across sensors. We observed this assumption is violated in our baseline data, where spurious sequenceness occasionally diverges in opposite directions at specific time lags (e.g., ~90 ms). In such instances, subtraction would increase the false-positive rate rather than suppress noise. In Figure 3B, we prioritized the comparison of pre-task versus post-task sequenceness within the same direction, as oscillatory confounds appeared more stable across time within a single direction, as opposed to across directions within a single session. However, we consider both approaches are valid. We now provide the fwd-bkw plots for completeness and comparison with previous literature. A) forward minus backwards sequenceness for Control (left) and Post-Learning resting-state (right). B) T-value distribution of the sign-flip permutation test for Control (left) and Post-Learning resting-state (right)”

(2) Relatedly, while the authors note that smaller time windows are necessary for TDLM to succeed, a more precise description of the appropriate window size would greatly improve the utility of this paper. As it stands, the discussion feels incomplete without this information, as providing explicit guidance on optimal window sizes would help future researchers apply TDLM effectively. Under what window size range can physiological levels of replay actually be detected using TDLM? Or, is there some scaling factor that should be considered, in terms of window size and significance threshold/replay density? If the authors are unable to provide a concrete recommendation, they could add information about time windows used in previous studies (perhaps, is 1500ms as used in their previous paper a good recommendation?).

We currently do not have an empirical estimate of which window sizes are appropriate. While we used 1500ms in our previous paper, this was solely given by the experiment design which had a 1.5s wait period before the next stimulus. Our recommendation for best guidance on this matter would be to investigate related intracranial literature for SWR rate increases under similar experimental conditions. We have added the following paragraph to the discussion:

“At this stage we cannot offer a general recommendation for window sizes as they are likely to depend on details of the research paradigm. However, intracranial recordings can be used as proxy to estimate the duration of replay bursts, for example as reported in (Norman et al., 2019) where increased SWRs were seen up to 1500 ms after retrieval cue onset”

(3) In their simulation, the authors define a replay event as a single transition from one item to another (example: A to B). However, in rodents, replay often traverses more than a single transition (example: A to B to C, even to D and E). Observing multistep sequences increases confidence that true replay is present. How does sequence length impact the authors' conclusions? Similarly, can the authors comment on how the length of the inserted events impacts TDLM sensitivity, if at all?

Good point! So far, most papers do not seem to include multi-step TDLM and in our experience rightfully, as it is conceptionally difficult to define clear significance thresholds while keeping in mind that shorter sub-sequences are contained within a longer sequence (e.g. ABC contains both AB and BC and a longer dependency of AC) that renders it difficult to define the correct way to create a null distribution for the permutation test. Therefore, we tried to stay as close as possible to previous approaches and only looked for single-step transitions. Nevertheless, we have added an analysis to the supplement comparing how TDLM behaves if we simulate A->B->C or A->B and separate B->C. It shows that TDLM is only sensitive to the number of transitions present in the data, and it does not matter if they are chained or chunked. The segment reads:

“We intentionally designed our study to encourage replay of triplets. However, this begs the question as to whether it matters if triplets or individual chunks of a sequence are replayed at different time points? Here, we simulated two scenarios. In one, we inserted replay of single transitions alone with a refractory period, e.g. A->B and separate B->C transitions. In a second scenario, we simulate replay of chained triplets, e.g. A->B->C, with a distance of 80 milliseconds each. Importantly, we kept the number of transitions constant (i.e., A->B, … B->C and where A->B->C would both have 2 transitions. This creates a context wherein a four-minute resting state would have ~100 events of A->B->C inserted and ~200 events of A->B or B->C, such that in both cases this results in the same number of single step transitions. We found both are equivalent, with TDLM agnostic to the length of sequence trains, i.e., it does not matter if replay is chunked or chained under the assumption that the number of transitions remains fixed, as can be seen in Appendix A Figure 2”

And the reference Figure description reads:

“TDLM is invariant to the length of sequence replay trains under an assumption that the number of target transitions (e.g. single steps) is fixed. We simulated replay either as two temporally separate A->B, B->C events (light orange/green) or as a single A>B->C event (dark orange/green), both yielding equivalent sequenceness. Shaded areas denote the standard error across participants”

For example, regarding sequence length, is it possible that TDLM would detect multiple parts of a longer sequence independently, meaning that the high density needed to detect replay is actually not quite so dense? (example: if 20 four-step sequences (A to B to C to D to E) were sampled by TDLM such that it recorded each transition separately, that would lead to a density of 80 events/min).

Indeed, this is an interesting proposal. We intentionally kept our simulation close to the way previous simulations were set-up (i.e. Liu & Dolan et al 2021, Liu & Mattar 2021) by simulating one-step transitions and simulated them such that there is no overlap between separate events (e.g. by defining a refractory period). If the duration of replay is increased then we would also need to increase the length of the refractory period, resulting in a reduced upper limit of how much replay can occur in a 1-minute time window. This in turn would approximate roughly the same number of transitions that can be inserted into the resting state and, as detailed above, would yield the same results. Nevertheless, as we chose to use replay density and not transition density as a marker, the density would be reduced, even if the number of transitions stay the same. We have added an analysis using multi-step replay to the supplement and discuss its implications and caveats. In the main discussion we have added the following segment:

“Similarly, in our simulation, for simplicity and to keep consistency with previousstimulations, we restricted replay events to span two reactivation events. While the characteristics of replay as measured by TDLM are unknown, it is conceivable that several steps can be replayed within one replay event. We show that the vanilla version of TDLM is fundamentally sensitive to the number of single-step transitions alone, and disregards if these are replayed chained or chunked (Appendix A.2 and Appendix A Figure 2). Nevertheless, if the number of reactivation events chained within a replay event increases, TDLMs sensitivity is increased relative to the replay density and thresholds are reached earlier (see Appendix A Figure 4). See Appendix A.4 for a simulation of multi-step replay events and our discussion of the caveats.”

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Please label the various significance thresholds in the legend of Figure 3.

We have labelled all the thresholds in the figure legends.

Reviewer #2 (Recommendations for the authors):

I think that some of the clarity is hampered because there is a bit too much reliance on explanations from the previous paper using this task, which hampers clarity in the paper. For example, Figure 1 is not particularly useful for understanding the study in its current form; I found myself relying almost exclusively on Supplementary Figure 1 (which is from the previous paper). I'd recommend presenting some version of SF1 in the main text instead. Another example of this overreliance on the previous paper is that, as far as I can tell, the present paper never explicitly states which transitions are being tested in TDLM. In the prior work, it states "all allowable graph transitions", and so I assumed this was the same here, but the paper should standalone without having to go back to the other study. I'd recommend that the authors revise the paper in these and other places where the previous paper is mentioned.

Thanks for raising this point! We were uncertain ourselves how to deal with the overlap in content and did not want to bloat the paper or plagiarize ourselves too much. On the advice of the referee have implemented the following to improve the manuscript and reduce a reliance on the previous paper:

Supplement Figure 1 is indeed crucial to understanding the experiment. We have moved it to the methods section under Methods: Procedure

Added more stimulus description to the Methods: Localizer section

Included more details about the localizer and graph learning that were missing before

We have added the note about which transitions we were looking for in the Methods section. Additionally, we have added this information to the Results section of Study 1.

There are also a few typos I noticed:

(1) Line 73: "during in the context of."

(2) Line 287: " to exploring the."

We fixed the typos.

Reviewer #3 (Recommendations for the authors):

(1) Why did the authors choose an 80ms state-to-state time lag for their simulation? I believe they should make the reason for this decision clear in the main text.

Indeed, this point was also raised by the other reviewer. We have added a sentence to the main text about the rationale behind this decision:

“We chose this timepoint (80 millisecond state-to-state lag) as its sequenceness value was close to zero in the baseline condition as well as being distant to the observed alpha rhythms of the participants (which varied between ~9-11 Hz). Additionally, we subtracted the mean sequenceness value of the baseline at 80 millisecond lag such that any simulation effects would, on average, start at zero sequenceness.“

Additionally, we have added some further explanation to the Methods section.

“This time lag (80 msec) was chosen in order to isolate precisely an effect of the experimentally inserted sequenceness. Thus, we chose a lag at which the mean baseline sequenceness was close to zero and where the correlation with behaviour was low. Additionally, we subtracted the mean sequenceness value (at 80 milliseconds) at baseline from the specific lag recorded for each participant, such that simulation effects would be initialized at zero sequenceness on average enabling any effects to be attributed purely to inserted replay. Additionally, we excluded time lags too close to the alpha rhythms of participants (which varied between ~9-11 Hz) or lags which would have a harmonic with the rhythm.“

(2) Line 168: Can the authors define what these conservative and liberal criteria are in the text?

We have added definitions of the criteria in the text. The text now reads:

“[..] significance thresholds (conservative, i.e. the maximum sequenceness across all permutations and timepoints or liberal criteria, i.e. the 95% percentile of aforementioned sequenceness).”

(3) Line 478: "calculate" instead of "calculated".

(4) Figure 7 D: y-axis is labeled "70 ms" I believe it should be labeled 80 ms.

Thanks, we fixed the two typos.

(5) With replay defined as sequential reactivation at a compressed temporal timescale, many of the iEEG citations (lines 54-55) do not demonstrate replay (they show stimulus reinstatement or ripple activity, but not sequential replay). Replay studies in humans using intracranial methods have been mostly limited to those measuring single-unit activity, a good example being Vaz et al., 2020 (https://www.science.org/doi/10.1126/science.aba0672).

We agree that, under a strict definition articulated by Genzel et al. that defines replay as sequential reactivation, many prior human iEEG studies are better described as stimulus reinstatement or ripple-related activity rather than true sequence replay. We have revised the text accordingly and now highlight the few intracranial microelectrode studies that demonstrate replay of firing sequences at the cellular/ensemble level in humans (Eichenlaub et al., 2020; Vaz et al., 2020), distinguishing these from macro-scale iEEG work providing indirect evidence alone.

The revised paragraph now reads:

“Replay has been shown using cellular recordings across a variety of mammalian model organisms (Hoffman & McNaughton, 2002; Lee & Wilson, 2002; Pavlides & Winson, 1989). Replay studies in humans using intracranial recordings are few, but include work demonstrating compressed replay of firing-pattern sequences in motor cortex during rest (Eichenlaub et al., 2020) as well as single-unit replay of trialspecific cortical spiking sequences during episodic retrieval (Vaz et al., 2020). By contrast, most iEEG studies report stimulus-specific reinstatement or ripple-locked activity changes without explicit demonstration of temporally compressed sequential replay (Axmacher et al., 2008; Staresina et al., 2015). As these methods are only applied under restricted clinical circumstances, such as during pre-operative neurosurgical assessments, this limits opportunities to investigate human replay. Therefore, this gives urgency to efforts aimed at developing novel methods to investigate human replay non-invasively.”

(6) The expectations about replay frequency are grounded in literature on hippocampal replay sequences. However, MEG captures signals from across the entire brain, and the hippocampal contribution is likely relatively weak compared to all other signals. This raises an important question: is TDLM genuinely unable to detect replay at physiological (i.e., hippocampal) levels, or is it instead detecting a different form of sequential reactivation - possibly involving cortex or other regions - that may occur more frequently? More broadly, when we have evidence of replay from TDLM, do we believe it is the same thing as replay of CA1 place cell spiking sequences, as detected in rodents? Commenting on this distinction would help further develop theories of replay and what TDLM is measuring.

This is indeed an important point that has garnered relatively little attention. While there is some evidence of a relation to hippocampal replay in form of high-frequency power increase in the hippocampus, ultimately it is not possible to know without intracranial recordings, as signal strength from those regions is rather poor in MEG.

We have added the following segment to the manuscript that discusses these issues:

“However, while we are using indices of SWRs as a proxy for replay density estimation, the relationship between hippocampal replay and replay detected by TDLM remains uncertain. While current decoding approaches measure replay-like phenomena on cortical sites, previous papers have reported a power increase in hippocampal areas coinciding with replay episodes as detected by TDLM. Nevertheless, it is conceivable that cortical replay found by TDLM could occur independently of hippocampal replay and SWRs and be generated by different mechanisms. Some TDLM-studies find a replay state-to-state time lag of above 100 ms, much slower than e.g. previously reported place cell replay. Future studies should employ simultaneous intracranial and cortical surface recordings to establish the relationship between hippocampal replay and replay found by TDLM.”

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Zeng et al. have investigated the impact of inhibiting lactate dehydrogenase (LDH) on glycolysis and the tricarboxylic acid cycle. LDH is the terminal enzyme of aerobic glycolysis or fermentation that converts pyruvate and NADH to lactate and NAD+ and is essential for the fermentation pathway as it recycles NAD+ needed by upstream glyceraldehyde-3-phosphate dehydrogenase. As the authors point out in the introduction, multiple published reports have shown that inhibition of LDH in cancer cells typically leads to a switch from fermentative ATP production to respiratory ATP production (i.e., glucose uptake and lactate secretion are decreased, and oxygen consumption is increased). The presumed logic of this metabolic rearrangement is that when glycolytic ATP production is inhibited due to LDH inhibition, the cell switches to producing more ATP using respiration. This observation is similar to the well-established Crabtree and Pasteur effects, where cells switch between fermentation and respiration due to the availability of glucose and oxygen. Unexpectedly, the authors observed that inhibition of LDH led to inhibition of respiration and not activation as previously observed. The authors perform rigorous measurements of glycolysis and TCA cycle activity, demonstrating that under their experimental conditions, respiration is indeed inhibited. Given the large body of work reporting the opposite result, it is difficult to reconcile the reasons for the discrepancy. In this reviewer's opinion, a reason for the discrepancy may be that the authors performed their measurements 6 hours after inhibiting LDH. Six hours is a very long time for assessing the direct impact of a perturbation on metabolic pathway activity, which is regulated on a timescale of seconds to minutes. The observed effects are likely the result of a combination of many downstream responses that happen within 6 hours of inhibiting LDH that causes a large decrease in ATP production, inhibition of cell proliferation, and likely a range of stress responses, including gene expression changes.

Strengths:

The regulation of metabolic pathways is incompletely understood, and more research is needed, such as the one conducted here. The authors performed an impressive set of measurements of metabolite levels in response to inhibition of LDH using a combination of rigorous approaches.

Weaknesses:

Glycolysis, TCA cycle, and respiration are regulated on a timescale of seconds to minutes. The main weakness of this study is the long drug treatment time of 6 hours, which was chosen for all the experiments. In this reviewer's opinion, if the goal was to investigate the direct impact of LDH inhibition on glycolysis and the TCA cycle, most of the experiments should have been performed immediately after or within minutes of LDH inhibition. After 6 hours of inhibiting LDH and ATP production, cells undergo a whole range of responses, and most of the observed effects are likely indirect due to the many downstream effects of LDH and ATP production inhibition, such as decreased cell proliferation, decreased energy demand, activation of stress response pathways, etc.

We thank reviewer for the careful reading of our manuscript, the accurate summary of the prevailing model, and the positive assessment of the rigor of our measurements. We agree that much prior literature reports increased oxygen consumption following LDH inhibition, and we recognize that our finding—coordinated suppression of glycolysis, the TCA cycle, and OXPHOS—differs from this prevailing interpretation. We address below the reviewer’s main concern regarding the 6-hour time point and clarify the conceptual scope of our study.

(1) Scope: steady-state metabolic regulation versus immediate transient effects

The reviewer raises an important point that many metabolic perturbations can trigger rapid, transient responses within seconds to minutes, whereas our measurements were performed after sustained LDH inhibition. We agree that very early time points would be required if the primary goal were to isolate the most immediate, proximal consequence of LDH inhibition before downstream propagation. However, the objective of our study is different: we aim to characterize the metabolic steady state re-established after sustained inhibition of LDH activity, because this adapted steady state is more relevant for understanding long-term metabolic consequences and therapeutic outcomes of LDH inhibition in cancer cells.

(2) Genetic LDHA/LDHB knockout: comparison of two steady states

A related point applies to the LDHA/LDHB knockout models. We fully agree that the knockout process necessarily involves a temporal perturbation during cell line generation and adaptation. Nevertheless, the experimental comparison in our study is explicitly between two steady states: the baseline steady state of control cells and the steady state achieved after stable genetic disruption of LDHA or LDHB. The observation that LDHA or LDHB knockout alone had minimal effects on glycolysis and respiration indicates that partial reduction of LDH activity can be compensated in a steady-state manner, consistent with the exceptionally high catalytic capacity of LDH in cancer cells relative to upstream rate-limiting enzymes.

(3) LDH-activity-dependent quantitative relationships support stable metabolic states

Importantly, our conclusions do not rely on a single inhibitor condition at a single time point. Rather, we established quantitative steady-state relationships between residual LDH activity and pathway behavior across a wide range of LDH inhibition. These LDH-activity-dependent data strongly support that the system resides in stable metabolic states at different degrees of LDH activity, rather than reflecting non-specific collapse due to prolonged stress.

Specifically, we observed that when LDH activity was reduced from 100% to approximately ~9% (e.g., by genetic perturbation and partial pharmacologic inhibition), glucose consumption and lactate production remained essentially unchanged, indicating maintenance of a steady-state glycolytic flux despite substantial LDH inhibition. Only when LDH activity was further reduced below this threshold did glycolytic flux decrease in a graded manner, consistent with a nonlinear control structure (Figure 8 A & B)).

Likewise, the isotope tracing results showed distinct LDH-activity-dependent transitions in TCA cycle labeling patterns. Over the range in which LDH activity decreased from 100% to ~9%, the [¹³C₆]glucose-derived labeling pattern of citrate remained largely unchanged, whereas deeper inhibition led to a decrease in m2 citrate with a compensatory rise in higher-order citrate isotopologues, consistent with altered flux entry versus cycling/retention in the TCA cycle (Figure 8C). Similarly, [¹³C₅]glutamine tracing revealed that deeper LDH inhibition reduced the direct m5 contribution, accompanied by corresponding shifts in other isotopologues (Figure 8D). These graded, quantitative transitions—rather than an abrupt global failure—support the interpretation of distinct metabolic steady states across LDH activity levels, linking LDH inhibition to changes in both glycolysis and mitochondrial metabolism.

(4) Reconciling discrepancies with prior studies

We agree that multiple prior studies have reported increased oxygen consumption or enhanced oxidative metabolism following LDH inhibition in cancer cells. However, we note that this prevailing notion often persists because LDH inhibition is frequently discussed by analogy to the classical Pasteur and Crabtree effects, in which cells toggle between fermentation and respiration depending on oxygen and glucose availability. We believe this analogy can be misleading.

In the Pasteur effect, the metabolic shift is primarily driven by oxygen limitation, i.e., restriction of the terminal electron acceptor for the mitochondrial electron transport chain, which enforces reliance on fermentation. In the Crabtree effect, high glucose availability suppresses respiration through regulatory mechanisms while glycolysis is strongly activated. Both phenomena are fundamentally controlled by oxygen availability and respiratory capacity, rather than by inhibition of a specific cytosolic enzyme.

By contrast, LDH inhibition is mechanistically distinct: it directly perturbs cytosolic redox recycling by limiting NADH-to-NAD⁺ regeneration and can therefore constrain upstream glycolytic flux (particularly at GAPDH) and reshape pathway thermodynamics. Under conditions where LDH inhibition sufficiently limits effective NAD⁺ availability and reduces glycolytic flux into pyruvate, the downstream consequence is reduced carbon input into the TCA cycle and suppressed OXPHOS—consistent with our experimental measurements. We therefore suggest that divergent outcomes reported across studies likely reflect differences in residual LDH activity, cell-type–specific metabolic wiring, and the extent to which glycolytic flux remains sustained versus becoming redox-limited upstream, rather than a universal Pasteur/Crabtree-like “switch” from fermentation to respiration. Accordingly, interpreting LDH inhibition as a Pasteur/Crabtree-like toggle may oversimplify the biochemical consequences of disrupting cytosolic NAD⁺ regeneration.

We have revised the Discussion to clarify this conceptual distinction and to avoid relying on comparisons that are not mechanistically equivalent to LDH inhibition.

Reviewer #2 (Public Review):

Summary:

Zeng et al. investigated the role of LDH in determining the metabolic fate of pyruvate in HeLa and 4T1 cells. To do this, three broad perturbations were applied: knockout of two LDH isoforms (LDH-A and LDH-B), titration with a non-competitive LDH inhibitor (GNE-140), and exposure to either normoxic (21% O2) or hypoxic (1% O2) conditions. They show that knockout of either LDH isoform alone, though reducing both protein level and enzyme activity, has virtually no effect on either the incorporation of a stable 13C-label from a 13C6-glucose into any glycolytic or TCA cycle intermediate, nor on the measured intracellular concentrations of any glycolytic intermediate (Figure 2). The only apparent exception to this was the NADH/NAD+ ratio, measured as the ratio of F420/F480 emitted from a fluorescent tag (SoNar).

The addition of a chemical inhibitor, on the other hand, did lead to changes in glycolytic flux, the concentrations of glycolytic intermediates, and in the NADH/NAD+ ratio (Figure 3). Notably, this was most evident in the LDH-B-knockout, in agreement with the increased sensitivity of LDH-A to GNE-140 (Figure 2). In the LDH-B-knockout, increasing concentrations of GNE-140 increased the NADH/NAD+ ratio, reduced glucose uptake, and lactate production, and led to an accumulation of glycolytic intermediates immediately upstream of GAPDH (GA3P, DHAP, and FBP) and a decrease in the product of GAPDH (3PG). They continue to show that this effect is even stronger in cells exposed to hypoxic conditions (Figure 4). They propose that a shift to thermodynamic unfavourability, initiated by an increased NADH/NAD+ ratio inhibiting GAPDH explains the cascade, calculating ΔG values that become progressively more endergonic at increasing inhibitor concentrations.

Then - in two separate experiments - the authors track the incorporation of 13C into the intermediates of the TCA cycle from a 13C6-glucose and a 13C5-glutamine. They use the proportion of labelled intermediates as a proxy for how much pyruvate enters the TCA cycle (Figure 5). They conclude that the inhibition of LDH decreases fermentation, but also the TCA cycle and OXPHOS flux - and hence the flux of pyruvate to all of those pathways. Finally, they characterise the production of ATP from respiratory or fermentative routes, the concentration of a number of cofactors (ATP, ADP, AMP, NAD(P)H, NAD(P)+, and GSH/GSSG), the cell count, and cell viability under four conditions: with and without the highest inhibitor concentration, and at norm- and hypoxia. From this, they conclude that the inhibition of LDH inhibits the glycolysis, the TCA cycle, and OXPHOS simultaneously (Figure 7).

Strengths:

The authors present an impressively detailed set of measurements under a variety of conditions. It is clear that a huge effort was made to characterise the steady-state properties (metabolite concentrations, fluxes) as well as the partitioning of pyruvate between fermentation as opposed to the TCA cycle and OXPHOS.

A couple of intermediary conclusions are well supported, with the hypothesis underlying the next measurement clearly following. For instance, the authors refer to literature reports that LDH activity is highly redundant in cancer cells (lines 108 - 144). They prove this point convincingly in Figure 1, showing that both the A- and B-isoforms of LDH can be knocked out without any noticeable changes in specific glucose consumption or lactate production flux, or, for that matter, in the rate at which any of the pathway intermediates are produced. Pyruvate incorporation into the TCA cycle and the oxygen consumption rate are also shown to be unaffected.

They checked the specificity of the inhibitor and found good agreement between the inhibitory capacity of GNE-140 on the two isoforms of LDH and the glycolytic flux (lines 229 - 243). The authors also provide a logical interpretation of the first couple of consequences following LDH inhibition: an increased NADH/NAD+ ratio leading to the inhibition of GAPDH, causing upstream accumulations and downstream metabolite decreases (lines 348 - 355).

Weaknesses:

Despite the inarguable comprehensiveness of the data set, a number of conceptual shortcomings afflict the manuscript. First and foremost, reasoning is often not pursued to a logical conclusion. For instance, the accumulation of intermediates upstream of GAPDH is proffered as an explanation for the decreased flux through glycolysis. However, in Figure 3C it is clear that there is no accumulation of the intermediates upstream of PFK. It is unclear, therefore, how this traffic jam is propagated back to a decrease in glucose uptake. A possible explanation might lie with hexokinase and the decrease in ATP (and constant ADP) demonstrated in Figure 6B, but this link is not made.

We appreciate the reviewer's critical comment. In Figure 3C, there is no accumulation of F6P or G6P, which are upstream of PFK1. This is because the PFK1-catalyzed reaction sets a significant thermodynamic barrier. Even with treatment using 30 μM GNE-140, the ∆G_PFK1 (Gibbs free energy of the PFK1-catalyzed reaction) remains -9.455 kJ/mol (Figure 3D), indicating that the reaction is still far from thermodynamic equilibrium, thereby preventing the accumulation of F6P and G6P.

We agree with the reviewer that hexokinase inhibition may play a role, this requires further investigation.

The obvious link between the NADH/NAD+ ratio and pyruvate dehydrogenase (PDH) is also never addressed, a mechanism that might explain how the pyruvate incorporation into the TCA cycle is impaired by the inhibition of LDH (the observation with which they start their discussion, lines 511 - 514).

We agree with the reviewer’s comment. In this study, we did not explore how the inhibition of LDH affects pyruvate incorporation into the TCA cycle. As this mechanism was not investigated, we have titled the study:

"Elucidating the Kinetic and Thermodynamic Insights into the Regulation of Glycolysis by Lactate Dehydrogenase and Its Impact on the Tricarboxylic Acid Cycle and Oxidative Phosphorylation in Cancer Cells."

It was furthermore puzzling how the ΔG, calculated with intracellular metabolite concentrations (Figures 3 and 4) could be endergonic (positive) for PGAM at all conditions (also normoxic and without inhibitor). This would mean that under the conditions assayed, glycolysis would never flow completely forward. How any lactate or pyruvate is produced from glucose, is then unexplained.

This issue also concerned me during the study. However, given the high reproducibility of the data, we consider it is true, but requires explanation. The PGAM-catalyzed reaction is tightly linked to both upstream and downstream reactions in the glycolytic pathway. In glycolysis, three key reactions catalyzed by HK2, PFK1, and PK are highly exergonic, providing the driving force for the conversion of glucose to pyruvate. The other reactions, including the one catalyzed by PGAM, operate near thermodynamic equilibrium and primarily serve to equilibrate glycolytic intermediates rather than control the overall direction of glycolysis, as previously described by us (J Biol Chem. 2024 Aug8;300(9):107648).

The endergonic nature of the PGAM-catalyzed reaction does not prevent it from proceeding in the forward direction. Instead, the directionality of the pathway is dictated by the exergonic reaction of PFK1 upstream, which pushes the flux forward, and by PK downstream, which pulls the flux through the pathway. The combined effects of PFK1 and PK may account for the observed endergonic state of the PGAM reaction.

However, if the PGAM-catalyzed reaction were isolated from the glycolytic pathway, it would tend toward equilibrium and never surpass it, as there would be no driving force to move the reaction forward.

Finally, the interpretation of the label incorporation data is rather unconvincing. The authors observe an increasing labelled fraction of TCA cycle intermediates as a function of increasing inhibitor concentration. Strangely, they conclude that less labelled pyruvate enters the TCA cycle while simultaneously less labelled intermediates exit the TCA cycle pool, leading to increased labelling of this pool. The reasoning that they present for this (decreased m2 fraction as a function of DHE-140 concentration) is by no means a consistent or striking feature of their titration data and comes across as rather unconvincing. Yet they treat this anomaly as resolved in the discussion that follows.

GNE-140 treatment increased the labeling of TCA cycle intermediates by [¹³C₆]glucose but decreased the OXPHOS rate, we consider the conflicting results as an 'anomaly' that warrants further explanation. To address this, we analyzed the labeling pattern of TCA cycle intermediates using both [¹³C₆]glucose and [¹³C₅]glutamine. Tracing the incorporation of glucose- and glutamine-derived carbons into the TCA cycle suggests that LDH inhibition leads to a reduced flux of glucose-derived acetyl-CoA into the TCA cycle, coupled with a decreased flux of glutamine-derived α-KG, and a reduction in the efflux of intermediates from the cycle. These results align with theoretical predictions. Under any condition, the reactions that distribute TCA cycle intermediates to other pathways must be balanced by those that replenish them. In the GNE-140 treatment group, the entry of glutamine-derived carbon into the TCA cycle was reduced, implying that glucose-derived carbon (as acetyl-CoA) entering the TCA cycle must also be reduced, or vice versa.

This step-by-step investigation is detailed under the subheading "The Effect of LDHB KO and GNE-140 on the Contribution of Glucose Carbon to the TCA Cycle and OXPHOS" in the Results section in the manuscript.

In the Discussion, we emphasize that caution should be exercised when interpreting isotope tracing data. In this study, treatment of cells with GNE-140 led to an increase labeling percentage of TCA cycle intermediates by [¹³C₆]glucose (Figure 5A-E). However, this does not necessarily imply an increase in glucose carbon flux into TCA cycle; rather, it indicates a reduction in both the flux of glucose carbon into TCA cycle and the flux of intermediates leaving TCA cycle. When interpreting the data, multiple factors must be considered, including the carbon-13 labeling pattern of the intermediates (m1, m2, m3, ---) (Figure 5G-K), replenishment of intermediates by glutamine (Figure 5M-V), and mitochondrial oxygen consumption rate (Figure 5W). All these factors should be taken into account to derive a proper interpretation of the data.

Reviewer #3 (Public Review):

Hu et al in their manuscript attempt to interrogate the interplay between glycolysis, TCA activity, and OXPHOS using LDHA/B knockouts as well as LDH-specific inhibitors. Before I discuss the specifics, I have a few issues with the overall manuscript. First of all, based on numerous previous studies it is well established that glycolysis inhibition or forcing pyruvate into the TCA cycle (studies with PDKs inhibitors) leads to upregulation of TCA cycle activity, and OXPHOS, activation of glutaminolysis, etc (in this work authors claim that lowered glycolysis leads to lower levels of TCA activity/OXPHOS). The authors in the current work completely ignore recent studies that suggest that lactate itself is an important signaling metabolite that can modulate metabolism (actual mechanistic insights were recently presented by at least two groups (Thompson, Chouchani labs). In addition, extensive effort was dedicated to understanding the crosstalk between glycolysis/TCA cycle/OXPHOS using metabolic models (Titov, Rabinowitz labs). I have several comments on how experiments were performed. In the Methods section, it is stated that both HeLa and 4T1 cells were grown in RPMI-1640 medium with regular serum - but under these conditions, pyruvate is certainly present in the medium - this can easily complicate/invalidate some findings presented in this manuscript. In LDH enzymatic assays as described with cell homogenates controls were not explained or presented (a lot of enzymes in the homogenate can react with NADH!). One of the major issues I have is that glycolytic intermediates were measured in multiple enzyme-coupled assays. Although one might think it is a good approach to have quantitative numbers for each metabolite, the way it was done is that cell homogenates (potentially with still traces of activity of multiple glycolytic enzymes) were incubated with various combinations of the SAME enzymes and substrates they were supposed to measure as a part of the enzyme-based cycling reaction. I would prefer to see a comparison between numbers obtained in enzyme-based assays with GC-MS/LC-MS experiments (using calibration curves for respective metabolites, of course). Correct measurements of these metabolites are crucial especially when thermodynamic parameters for respective reactions are calculated. Concentrations of multiple graphs (Figure 1g etc.) are in "mM", I do not think that this is correct.

We thank the reviewer’s comment and the following are clarification of the conceptual framework, the quantitative methodology, and the experimental basis supporting our conclusions.

(1) “It is well established that glycolysis inhibition or forcing pyruvate into the TCA cycle… leads to upregulation of TCA/OXPHOS… (authors claim lowered glycolysis leads to lower TCA/OXPHOS)”

This framing is not accurate in the context of our study. PDK inhibition and LDH inhibition are fundamentally different perturbations. PDK inhibition directly promotes mitochondrial pyruvate oxidation by enabling PDH flux, whereas LDH inhibition primarily perturbs cytosolic redox balance (free NADH/NAD⁺) and thereby constrains upstream glycolytic reactions, particularly the GAPDH step. Therefore, the metabolic outcomes of these interventions are not expected to be identical and should not be treated as interchangeable.

Importantly, we do not “ignore” prior studies proposing increased OXPHOS after LDH inhibition; we explicitly cite and summarize this prevailing interpretation in the Introduction. Our study was motivated precisely because this interpretation does not resolve key quantitative inconsistencies, including (i) the large mismatch between glycolytic flux and mitochondrial oxidative capacity, and (ii) the exceptionally high catalytic capacity of LDH relative to upstream rate-limiting glycolytic enzymes. These constraints raise a mechanistic question: how does LDH inhibition actually suppress glycolytic flux in intact cancer cells, and what are the consequences for TCA cycle and OXPHOS?

Our central contribution is the identification of a biochemical mechanism supported by integrated measurements of fluxes, metabolite concentrations, redox state, and reaction thermodynamics: LDH inhibition increases free NADH/NAD⁺, decreases free NAD⁺ availability, inhibits GAPDH, drives accumulation/depletion patterns in glycolytic intermediates, shifts Gibbs free energies of near-equilibrium reactions (PFK1–PGAM segment), suppresses pyruvate production, and consequently reduces carbon input into TCA cycle and OXPHOS. These analyses are not provided by most prior work and directly address the mechanistic gap.

(2) Lactate signaling (Thompson/Chouchani) and metabolic modeling (Titov/Rabinowitz)

These research directions are valuable, but they address questions that are different from the one investigated here. Our manuscript focuses on steady-state biochemical control of metabolic flux by LDH inhibition through redox-linked kinetics and pathway thermodynamics.

(3) Pyruvate in RPMI

Pyruvate in standard medium does not invalidate our conclusions. All experimental comparisons were performed under identical conditions across groups, and the major conclusions rely on orthogonal measurements including glycolytic flux (glucose consumption/lactate production), OCR profiling, and isotope tracing with [¹³C₆]glucose and [¹³C₅] glutamine, which directly quantify carbon entry into lactate and TCA cycle intermediates. These tracer-based results are not confounded by unlabeled extracellular pyruvate in a way that would reverse the mechanistic conclusions.

(4) LDH activity assay in homogenates and “many enzymes can react with NADH”

This concern is overstated. In the LDH assay, substrates are pyruvate + NADH, and the measured signal reflects NADH oxidation coupled to pyruvate reduction. In cell lysates, LDH is uniquely abundant and catalytically efficient for this reaction pair, and the inhibitor-response behavior matches the known LDHA/LDHB selectivity of GNE-140 and the cellular phenotypes. Thus, the assay is mechanistically specific in this context.

(5) Enzyme-coupled metabolite assays and request for LC–MS validation

The reviewer’s implication that enzyme-coupled assays are intrinsically unreliable is incorrect. Enzymatic cycling assays are a widely used quantitative approach when performed with proper specificity and calibration, and they are particularly useful for labile glycolytic intermediates that are challenging to quantify reproducibly by MS without specialized quenching, derivatization, and isotope dilution standards.

We agree that MS-based quantification is valuable, and we have developed LC–MS methods for selected metabolites. However, absolute quantification of these intermediates remains technically difficult due to the inherent limitation of this method and, in our hands, did not provide uniformly robust performance for all intermediates required for thermodynamic analysis.

(6) Units (“mM”)

The metabolite concentration units are correct.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

If the goal is to investigate the direct impact of LDH inhibition, then in my opinion, most of these experiments need to be repeated at a very early time point immediately after or a few minutes after LDH inhibition. I understand that this is a tremendous amount of work that the authors might not want to pursue. I do want to highlight that the quality of the experiments performed in this work is impressive. I hope the authors continue investigating this subject and look forward to reading their future manuscripts on this topic.

We thank the reviewer for this thoughtful and constructive comment and for the positive assessment of the experimental quality of our work.

We fully agree that measurements at very early time points after LDH inhibition would be required if the goal were to isolate an immediate, proximal molecular event occurring before downstream propagation. However, the primary objective of our study is not to dissect a single instantaneous biochemical consequence of LDH inhibition, but rather to characterize the metabolic steady state that is re-established after sustained suppression of LDH activity, which we believe is more relevant for understanding the long-term metabolic and therapeutic consequences of LDH inhibition in cancer cells.

(1) Scope: steady-state metabolic regulation versus immediate transient effects

The reviewer raises an important point that many metabolic perturbations can trigger rapid, transient responses within seconds to minutes, whereas our measurements were performed after sustained LDH inhibition. We agree that very early time points would be required if the primary goal were to isolate the most immediate, proximal consequence of LDH inhibition before downstream propagation. However, the objective of our study is different: we aim to characterize the metabolic steady state re-established after sustained inhibition of LDH activity, because this adapted steady state is more relevant for understanding long-term metabolic consequences and therapeutic outcomes of LDH inhibition in cancer cells.

(2) Genetic LDHA/LDHB knockout: comparison of two steady states

A related point applies to the LDHA/LDHB knockout models. We fully agree that the knockout process necessarily involves a temporal perturbation during cell line generation and adaptation. Nevertheless, the experimental comparison in our study is explicitly between two steady states: the baseline steady state of control cells and the steady state achieved after stable genetic disruption of LDHA or LDHB. The observation that LDHA or LDHB knockout alone had minimal effects on glycolysis and respiration indicates that partial reduction of LDH activity can be compensated in a steady-state manner, consistent with the exceptionally high catalytic capacity of LDH in cancer cells relative to upstream rate-limiting enzymes.

(3) LDH-activity-dependent quantitative relationships support stable metabolic states

Importantly, our conclusions do not rely on a single inhibitor condition at a single time point. Rather, we established quantitative steady-state relationships between residual LDH activity and pathway behavior across a wide range of LDH inhibition. These LDH-activity-dependent data strongly support that the system resides in stable metabolic states at different degrees of LDH activity, rather than reflecting non-specific collapse due to prolonged stress.

Specifically, we observed that when LDH activity was reduced from 100% to approximately ~9% (e.g., by genetic perturbation and partial pharmacologic inhibition), glucose consumption and lactate production remained essentially unchanged, indicating maintenance of a steady-state glycolytic flux despite substantial LDH inhibition. Only when LDH activity was further reduced below this threshold did glycolytic flux decrease in a graded manner, consistent with a nonlinear control structure.

Likewise, the isotope tracing results showed distinct LDH-activity-dependent transitions in TCA cycle labeling patterns. Over the range in which LDH activity decreased from 100% to ~9%, the [¹³C₆]glucose-derived labeling pattern of citrate remained largely unchanged, whereas deeper inhibition led to a decrease in m2 citrate with a compensatory rise in higher-order citrate isotopologues, consistent with altered flux entry versus cycling/retention in the TCA cycle. Similarly, [¹³C₅]glutamine tracing revealed that deeper LDH inhibition reduced the direct m5 contribution, accompanied by corresponding shifts in other isotopologues. These graded, quantitative transitions—rather than an abrupt global failure—support the interpretation of distinct metabolic steady states across LDH activity levels, linking LDH inhibition to changes in both glycolysis and mitochondrial metabolism.

Reviewer #2 (Recommendations For The Authors):

All in all, the authors would benefit from collaboration with a group more well-versed in quantitative aspects of metabolism (such as Metabolic Control Analysis) and modelling methods (such as flux analysis) to boost the interpretation and impact of their really nice data set.

We sincerely thank the reviewer for this insightful and constructive suggestion. We fully agree that collaboration with groups specializing in quantitative metabolic analysis, such as Metabolic Control Analysis and flux modeling, would further expand the interpretative depth and broader impact of this work.

The primary objective of the present work, however, was not to construct a global mathematical model, but to experimentally dissect the biochemical mechanism by which LDH inhibition coordinately suppresses glycolysis, the TCA cycle, and OXPHOS, integrating enzyme kinetics with thermodynamic constraints at steady state. Within this scope, we focused on experimentally demonstrable relationships between LDH activity, redox balance, GAPDH perturbation, thermodynamic shifts in near-equilibrium reactions, and emergent flux suppression.

We fully recognize the power of MCA and related modeling approaches in formalizing control coefficients and system-level sensitivities, and we view our dataset as particularly well suited to support such future analyses. We therefore see this work as providing a robust experimental platform upon which more comprehensive quantitative modeling can be built, either in future studies or through collaboration with specialists in metabolic modeling.

Reviewer #3 (Recommendations For The Authors):

We sincerely thank the reviewer for the important suggestions.

(1) I strongly disagree that "regulation of glycolytic flux".. "remained largely unexplored.”

Our original wording was meant to emphasize not the absence of prior work on glycolytic flux regulation, but rather that the specific biochemical mechanism by which LDH regulates glycolytic flux—particularly through the integrated effects of enzyme kinetics, redox balance, and thermodynamic constraints within the pathway—has not been fully elucidated.

To avoid any ambiguity or overstatement, we have revised the relevant text to more precisely reflect this intent. The revised wording now reads:

“This study elucidates a biochemical mechanism by which lactate dehydrogenase influences glycolytic flux in cancer cells, revealing a kinetic–thermodynamic interplay that contributes to metabolic regulation.”

We believe this revised phrasing more accurately acknowledges prior work while clearly defining the specific mechanistic contribution of the present study.

(2) Very confusing in the Introduction section: "If LDH is inhibited at the LDH step..”

We sincerely thank the reviewer for pointing out the potential confusion caused by the phrase “If LDH is inhibited at the LDH step” in the Introduction.

Our intention was to contrast two conceptual models of LDH inhibition. The first is the conventional view, in which the effect of LDH inhibition is assumed to be confined to the LDH-catalyzed reaction itself, leading primarily to local accumulation of pyruvate and its redirection toward mitochondrial metabolism. The second, which is supported by our data, is that LDH inhibition initiates a system-wide biochemical response, perturbing redox balance, upstream enzyme kinetics, and the thermodynamic state of the glycolytic pathway, ultimately resulting in coordinated suppression of glycolysis, the TCA cycle, and OXPHOS.

We agree that the original phrasing was ambiguous and potentially misleading. To improve clarity, we have revised the text as follows:

“If the effect of LDH inhibition were confined solely to its catalytic step…”

(3) The entire introduction part when the authors attempt to explain how decreased glycolysis will lead to decreased mitochondrial respiration is confusing.

We would like to clarify that the Introduction does not attempt to explain how decreased glycolysis leads to decreased mitochondrial respiration. Rather, the final paragraph of the Introduction is intended to highlight an unresolved conceptual inconsistency in the existing literature and to motivate the central question addressed in this study.

Specifically, we summarize the prevailing view that LDH inhibition redirects pyruvate toward mitochondrial metabolism and enhances oxidative phosphorylation, and then point out that this interpretation is difficult to reconcile with quantitative considerations, such as the large disparity between glycolytic and mitochondrial flux capacities and the excess catalytic activity of LDH relative to upstream glycolytic enzymes. These observations are presented to emphasize that the biochemical mechanism linking LDH inhibition to changes in glycolysis and mitochondrial respiration has not been fully resolved.

Importantly, the Introduction does not propose a mechanistic explanation for the observed suppression of mitochondrial respiration; rather, it poses this as an open question, which is then systematically addressed through experimental analysis in the Results section.

(4) Line 144: "which is 81(HeLa-LDHAKO) -297(HeLa-Ctrl) times"- here and in many other places wording is confusing to the reader.

Our intention was to emphasize the significant redundancy of LDH activity relative to hexokinase (HK), the first rate-limiting enzyme in the glycolysis pathway, in cancer cells.

Specifically, we wanted to express that in HeLa-Ctrl cells, the total LDH activity is 297 times that of HK activity; while in HeLa-LDHAKO cells, although the total LDH activity decreased, it was still 81 times that of HK activity. This data comes from supplement Table 1 in the paper and aims to provide quantitative evidence for "why knocking out LDHA or LDHB alone is insufficient to significantly affect glycolysis flux," because the remaining LDH activity is still far higher than the HK activity at the pathway entrance, sufficient to maintain flux.

Based on your suggestion, we rewrite it in the revised draft with a more specific statement: "...the total activity of LDH in HeLa cells is very high, which is 297-fold higher than the first rate-limiting enzyme HK activity in HeLa-Ctrl cells and 81-fold higher in HeLa-LDHAKO cells.”

(5) Line 153: "in the following four aspects:"- but what are these aspects, the text below has no corresponding subtitles, etc.

Our intention was to indicate that after LDHA or LDHB knockout alone failed to affect the glycolysis rate, we further explored its potential impact on the glycolytic pathway from four deeper perspectives: the glucose carbon to pyruvate and lactate, the glucose carbon to subsidiary branches of glycolysis, the concentration of glycolytic intermediates and the thermodynamic state of the pathway, and the redox state of cytosolic free NADH/NAD⁺.

Following your valuable suggestion, we have now added the aforementioned clear subtitles to these four aspects in the revised manuscript.

(6) Lines 193, another example of the very confusing statement: "The results suggested that the loss of total LDH concentration was compensated.."

The actual catalytic activity (reaction rate) of LDH is determined by both its enzyme concentration and substrate concentration (pyruvate and NADH). When the total LDH protein concentration (enzyme amount) in the cell is reduced through gene knockout, the reaction equilibrium is disrupted. To maintain sufficient lactate production flux to support a high glycolysis rate, the cell compensates by increasing the concentration of one of the substrates—free NADH (as shown in Figure 1I). This results in an increased substrate concentration, despite a reduction in the amount of enzyme, thus partially maintaining the overall reaction rate.

We have revised the original statement to more accurately describe this kinetic equilibrium process: "The decrease in total LDH concentration was counterbalanced by a concomitant increase in the concentration of its substrate, free NADH, thereby maintaining the reaction velocity.”

(7) Line 222-223: "did not or marginally significantly affect....”

Our intention is to reflect the complexity of the data in Figure 1. Specifically: Regarding "did not affect": This means that there were no statistically significant differences in most key parameters, such as glycolytic flux (glucose consumption rate, lactate production rate). Regarding "or marginally significantly affected": This means that in a few indicators, although statistical calculations showed p-values less than 0.05, the absolute value of the difference was very small, with limited biological significance.

To clarify this, we rewrite it as: "...did not significantly affect glucose-derived pyruvate entering into TCA cycle, neither significantly affect mitochondrial respiration, although statistically significant but minimal changes were observed in a few specific parameters (e.g., m3-pyruvate% in medium).”

(8) It is very confusing to use the same colors for three GNE-140 drug concentrations (Figure 2a-b) and for 3 different cell lines right next to each other (Figure 2c-d).

The figures have been revised accordingly.

(9) Lines 263-273: nothing is new here as oxidized NAD+ is required for run glycolysis and LDH inhibition/KO leads to a high NADH/NAD+ ratio; Also below it is well known that reductive stress blocks serine biosynthesis;

It is well established that oxidized NAD⁺ is required for glycolysis, that LDH inhibition or knockout increases the NADH/NAD⁺ ratio, and that reductive stress can suppress serine biosynthesis. We did not intend to present these observations as novel.

The key point of this section is not the qualitative requirement of NAD⁺ for GAPDH, but rather the mechanistic alignment between LDH inhibition, changes in free NAD⁺ availability, and the emergence of GAPDH as a flux-controlling step within the glycolytic pathway under steady-state conditions. Previous studies have largely treated the increase in NADH/NAD⁺ following LDH inhibition as a correlative or downstream effect, without directly demonstrating how this redox shift quantitatively propagates upstream to reorganize glycolytic flux distribution and thermodynamic driving forces.

In our study, we explicitly link LDH inhibition to (i) an increase in free NADH/NAD⁺ ratio, (ii) inhibition of GAPDH activity in intact cells, (iii) accumulation of upstream glycolytic intermediates, (iv) suppression of serine biosynthesis from 3-phosphoglycerate, and critically, (v) coordinated shifts in the Gibbs free energies of reactions between PFK1 and PGAM. This integrated kinetic–thermodynamic framework goes beyond the established qualitative understanding of NAD⁺ dependence and provides a pathway-level mechanism by which LDH activity controls glycolytic flux.

(10) Lines 368-370: "... we reached an alternative interpretation of the data.."- does not provide much confidence.

Our intention was to prudently emphasize that we proposed a new interpretation based on detailed data, differing from conventional views. Our interpretation is grounded in key and consistent evidence from dual isotope tracing experiments using [¹³C₆]glucose and [¹³C₅]glutamine: The [¹³C₆]glucose tracing data: the labeling pattern of citrate, the starting product of TCA cycle, showed a significant decrease in m+2 %. This directly reflects a reduction in the flux of newly generated acetyl-CoA from glucose entering the TCA cycle. Simultaneously, the sum of other isotopologues % (m+1/ m+3/ m+4/m+5/m+6) increased, indicating a longer retention time of the labeled carbon in the cycle, implying a simultaneous decrease in the flux of cycle intermediates effluxed for biosynthesis. [¹³C₅]Glutamine tracing data: the labeling pattern of α-ketoglutarate showed a decrease in m+5 %, indicating a reduction in glutamine replenishment flux. The pattern of change in the total percentage of other isotopologues % (m+1/ m+2/ m+3/m+4) also supports the conclusion of reduced intermediate product efflux.

These two sets of data corroborate each other, pointing to a unified conclusion: LDH inhibition not only reduces carbon source inflow into the TCA cycle but also decreases intermediate product efflux, leading to a decrease in overall cycle activity. Therefore, our "alternative interpretation" is a well-supported and more consistent explanation of our overall experimental results. We revise the original wording to: "Integrated analysis of dual isotope tracing data demonstrates that LDH inhibition reduces both influx and efflux of the TCA cycle..."

(11) Lines 418-421: This entire discussion on how TCA cycle activity is decreased upon LDH inhibition is very confusing. I also would like to see these tracer studies when ETC is inhibited with different inhibitors.

We would like to clarify that the mitochondrial respiration rate data presented in Figure 5W are based on studies using different ETC inhibitors, and the cell treatment conditions (including culture time, etc.) for these oxygen consumption measurements are consistent with the conditions for the [¹³C₆]glucose and [¹³C₅]glutamine isotope tracing experiments (Figure 5A-V). Therefore, the changes in TCA cycle flux revealed by the tracing data and the inhibition of OXPHOS rate shown by the respiration measurements are mutually corroborating evidence from the same experimental conditions.

(12) Figure 6F, G - very limited representation of growth curves, why not perform these experiments with all corresponding cell lines and over multiple days. Especially since proliferation arrest vs cell death was implicated.

We have provided the growth curves of the HeLa-Ctrl and HeLa-LDHAKO cell lines under the corresponding treatments in Figure 6—figure supplement 1, as a supplement to Figure 6F, G (HeLa-LDHBKO cells). The choice of 48 hours as the cutoff observation point is based on clear biological evidence: under the stress of hypoxia (1% O₂) combined with GNE-140 treatment, HeLa-LDHBKO cells experienced substantial death within 24 to 48 hours, at which point the differences in the growth curves were already very significant.

(13) Move most of the Supplementary tables into an Excel file - so values can be easily accessed.

We have compiled the tables into an Excel file and submitted it along with the revised manuscript as supplementary material.

(14) Consider changing colors to more appealing- especially jarring is a bright blue, red, black combination on many bar graphs.

We have adjusted the color scheme of the figures (especially the bar graphs) in the paper, and have submitted them with the revised manuscript.

(15) Double check y-axis on multiple graphs it says "mM".

We have checked y-axis, the unit (mM) is correct.

(16) Instead TCA cycle use the TCA cycle.

In the revised manuscript, TCA cycle is used.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this manuscript, Chengjian Zhao et al. focused on the interactions between vascular, biliary, and neural networks in the liver microenvironment, addressing the critical bottleneck that the lack of high-resolution 3D visualization has hindered understanding of these interactions in liver disease.

Strengths:

This study developed a high-resolution multiplex 3D imaging method that integrates multicolor metallic compound nanoparticle (MCNP) perfusion with optimized CUBIC tissue clearing. This method enables the simultaneous 3D visualization of spatial networks of the portal vein, hepatic artery, bile ducts, and central vein in the mouse liver. The authors reported a perivascular structure termed the Periportal Lamellar Complex (PLC), which is identified along the portal vein axis. This study clarifies that the PLC comprises CD34⁺Sca-1⁺ dual-positive endothelial cells with a distinct gene expression profile, and reveals its colocalization with terminal bile duct branches and sympathetic nerve fibers under physiological conditions.

Comments on revisions:

The authors very nicely addressed all concerns from this reviewer. There are no further concerns or comments.

We sincerely thank the reviewer for the positive evaluation of the revised manuscript.

Reviewer #2 (Public review):

Summary:

The present manuscript of Xu et al. reports a novel clearing and imaging method focusing on the liver. The Authors simultaneously visualized the portal vein, hepatic artery, central vein, and bile duct systems by injected metal compound nanoparticles (MCNPs) with different colors into the portal vein, heart left ventricle, vena cava inferior and the extrahepatic bile duct, respectively. The method involves: trans-cardiac perfusion with 4% PFA, the injection of MCNPs with different colors, clearing with the modified CUBIC method, cutting 200 micrometer thick slices by vibratome, and then microscopic imaging. The Authors also perform various immunostaining (DAB or TSA signal amplification methods) on the tissue slices from MCNP-perfused tissue blocks. With the application of this methodical approach, the Authors report dense and very fine vascular branches along the portal vein. The authors name them as 'periportal lamellar complex (PLC)' and report that PLC fine branches are directly connected to the sinusoids. The authors also claim that these structures co-localize with terminal bile duct branches and sympathetic nerve fibers and contain endothelial cells with a distinct gene expression profile. Finally, the authors claim that PLC-s proliferate in liver fibrosis (CCl4 model) and act as scaffold for proliferating bile ducts in ductular reaction and for ectopic parenchymal sympathetic nerve sprouting.

Strengths:

The simultaneous visualization of different hepatic vascular compartments and their combination with immunostaining is a potentially interesting novel methodological approach.

Weaknesses:

This reviewer has some concerns about the validity of the microscopic/morphological findings as well as the transcriptomics results, and suggests that the conclusions of the paper may be critically viewed. Namely, at this point, it is still not fully clear that the 'periportal lamellar complex (PLC)' that the Authors describe really exists as a distinct anatomical or functional unit or these are fine portal branches that connect the larger portal veins into the adjacent sinusoid. Also, in my opinion, to identify the molecular characteristics of such small and spatially highly organized structures like those fine radial portal branches, the only way is to perform high-resolution spatial transcriptomics (instead of data mining in existing liver single cell database and performing Venn diagram intersection analysis in hepatic endothelial subpopulations). Yet, the existence of such structures with a distinct molecular profile cannot be excluded. Further research with advanced imaging and omics techniques (such as high resolution volume imaging, and spatial transcriptomics/proteomics) are needed to reproduce these initial findings.

We thank the reviewer for the thoughtful and constructive comments. In response to the reviewer’s concerns regarding the anatomical and molecular definition of the periportal lamellar complex (PLC), we have further clarified the scope and methodological boundaries of the present study in the revised manuscript.

Regarding the key question raised by the reviewer—namely, whether the PLC represents an independent anatomical or functional unit, or merely small portal venous branches connecting larger portal veins to adjacent sinusoids—we provide below a more detailed explanation of the criteria used to define the PLC in this study. The identification of the PLC is primarily based on periportal structures that can be reproducibly recognized by three-dimensional imaging across multiple mice, exhibiting a relatively consistent spatial distribution within the periportal region. The PLC could be stably observed across different MCNP dye color assignments and independent experimental batches. In addition, three-dimensional CD31 immunofluorescence consistently revealed vascular-associated signal distributions in the same periportal region, indirectly supporting its spatial association with the periportal vascular system.

At the morphological level, the PLC appears as a periportal vasculature-associated structure distributed around the main portal vein trunk and maintains a relatively consistent spatial proximity to portal veins, bile ducts, and neural components in three-dimensional space. This highly conserved spatial organization across multiple tissue systems supports the anatomical positioning of the PLC as a relatively distinct structural tissue unit within the periportal region.

The present study primarily focuses on a descriptive characterization of the three-dimensional anatomical organization and spatial relationships of the PLC based on volumetric imaging and vascular labeling strategies. As a complementary exploratory analysis, we reanalyzed endothelial cell populations potentially associated with the PLC using existing liver single-cell transcriptomic datasets. This analysis was intended to provide molecular-level information consistent with the structural observations and to offer preliminary clues to its potential biological functions, rather than to independently define the PLC at the spatial level or to functionally validate it.

We fully acknowledge the value of spatial transcriptomic and spatial proteomic technologies in revealing molecular heterogeneity within tissue architecture. However, under current technical conditions, these approaches are largely dependent on thin tissue sections and are limited by spatial resolution and signal mixing effects, which still pose challenges for resolving periportal structures with pronounced three-dimensional continuity, such as the PLC. In the future, further integration of high-resolution volumetric imaging with spatial omics technologies may enable a more refined understanding of the molecular features and potential functions of the PLC at higher spatial resolution.

Reviewer #3 (Public review):

Summary:

In the revised version of the manuscript authors addressed multiple comments, clarifying especially the methodological part of their work and PLC identification as a novel morphological feature of the adult liver portal veins. Tet is now also much clearer and has better flow.

The additional assessment of the smartSeq2 data from Pietilä et al., 2025 strengthens the transcriptomic profiling of the CD34+Sca1+ cells and the discussion of the possible implications for the liver homeostasis and injury response. Why it may suffer from similar bias as other scRNA seq datasets - multiple cell fate signatures arising from mRNA contamination from proximal cells during dissociation, it is less likely that this would happen to yield so similar results.

Nevertheless, a more thorough assessment by functional experimental approaches is needed to decipher the functional molecules and definite protein markers before establishing the PLC as the key hub governing the activity of biliary, arterial, and neuronal liver systems.

The work does bring a clear new insight into the liver structure and functional units and greatly improves the methodological toolbox to study it even further, and thus fully deserves the attention of the Elife readers.

Strengths:

The authors clearly demonstrate an improved technique tailored to the visualization of the liver vasulo-biliary architecture in unprecedented resolution.

This work proposes a new morphological feature of adult liver facilitating interaction between the portal vein, hepatic arteries, biliary tree, and intrahepatic innervation, centered at previously underappreciated protrusions of the portal veins - the Periportal Lamellar Complexes (PLCs).

Weaknesses:

The importance of CD34+Sca1+ endothelial cell subpopulation for PLC formation and function was not tested and warrants further validation.

We thank the reviewer for the careful and constructive comments regarding the functional validation of cell populations associated with the PLC. The central aim of this study is to establish and validate a novel volumetric imaging and vascular labeling strategy and to apply it to the periportal region of the liver, thereby revealing previously underappreciated structural organizational patterns at the three-dimensional level, rather than to perform a systematic functional validation of specific cellular subpopulations.

We agree that the precise roles of the CD34⁺Sca-1⁺ endothelial cell subpopulation in the formation and function of the periportal lamellar complex (PLC) have not been directly addressed through functional intervention experiments in the present study. Our conclusions are primarily based on three-dimensional imaging and spatial distribution analyses, which reveal a stable and consistent spatial association between this cell population and the PLC structure, but are not intended to independently support causal or functional inferences. The underlying functional mechanisms remain to be elucidated in future studies using genetic or functional perturbation approaches.

In light of these considerations, we have further refined the relevant statements in the revised manuscript to more clearly define the functional scope and limitations of the current study in the Discussion section, and to avoid functional interpretations that extend beyond the direct support of the data. At the same time, we consider functional validation of the PLC to be an important and promising direction for future investigation.

It should be emphasized that the present study is not primarily designed to provide direct functional validation, but rather to systematically characterize the three-dimensional structural features of the periportal lamellar complex (PLC) and its cellular associations using volumetric imaging and vascular labeling approaches. At this stage, we mainly provide spatial and histological evidence for the organizational relationship between the PLC structure and the CD34⁺Sca-1⁺ endothelial cell population, while their specific roles in PLC formation and functional regulation await further investigation.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

I highly appreciate the Authors' endeavors to improve the manuscript. I am enlisting those points (from my original review) where I still have further comments.

(2) I would suggest this sentence:

"...the liver has evolved a highly complex and densely organized ductal vascular-neuronal network in the body, consisting primarily of the portal vein system, central vein system, hepatic artery system, biliary system, and intrahepatic autonomic nerve network [6, 7]."

We thank the reviewer for the valuable suggestion. We have revised the relevant sentence accordingly, and the revised wording is as follows:

“The liver has evolved a highly complex and densely organized vascular–biliary–neural network, primarily composed of the portal venous system, central venous system, hepatic arterial system, biliary system, and the intrahepatic autonomic neural network.”

(3) I suggest renaming 'clearing efficiency' to 'clearing time', and revise the last sentence like:

'...The results showed that the average transmittance increased by 20.12% in 1mm-thick cleared tissue slices.'

We thank the reviewer for this helpful suggestion. Accordingly, we have replaced the term “clearing efficiency” with “clearing time” and revised the final sentence to reflect this change. The revised wording is as follows:

“The results showed that the average transmittance increased by 20.12% in cleared tissue slices with a thickness of 1 mm.”

(4) While the dye perfusion was indeed on full lobe, FigS1F also seems to be rather a thick section instead of a full 3d reconstruction. This is OK, but please, be clear and specific about this in the respective part of the ms.

We thank the reviewer for the careful review and detailed comments. We would like to clarify that Fig. S1F shows whole-lobe imaging of the mouse left liver lobe obtained after dye perfusion at the whole-liver scale, rather than an image derived from a thick tissue section. Although this image does not represent a three-dimensional reconstruction, it does reflect imaging of the entire left liver lobe at the macroscopic level.

In addition, for the reviewer’s reference, we have provided in this response a representative image of a 200 μm-thick liver tissue section to directly illustrate the morphological differences between thick-section imaging and whole-lobe imaging. We note that the third and fourth panels in Fig. 1G of the main text already show local imaging results from 200 μm-thick sections; in contrast, the comparative image provided here presents a larger field of view and overall morphology. To avoid redundancy, this additional image is included solely for clarification in the present response and has not been incorporated into the revised manuscript or the supplementary materials.

(11) Regarding the 'transmission quantification':

'Regarding the comparative quantification of different clearing methods, as the reviewer noted, nearly all aqueous or organic solvent based clearing techniques can achieve relatively uniform transparency in 1 mm thick tissue sections, so differences at this thickness are limited.'

So, based on all these, I think, measuring/comparisons of clearing efficacy in the present form are kind of pointless --- one may consider omitting this part.

We thank the reviewer for the valuable comments. The purpose of the transmittance quantification in this study was not to provide a comprehensive comparison among different tissue-clearing methods, but rather to serve as a quantitative reference supporting the optimization of the Liver-CUBIC protocol. Accordingly, we have narrowed and clarified the relevant statements in the revised manuscript to define their scope and avoid overinterpretation.

The revised text now reads as follows:

“Importantly, Liver-CUBIC treatment did not induce significant tissue expansion (Figure 1B–D). In addition, quantitative transmittance measurements in 1-mm-thick cleared tissue slices showed an average increase of 20.12% (P < 0.0001; 95% CI: 19.14–21.09; Figure 1E).”

Author response image 1.

(16) It is OK, but please, indicate this clearly in the Methods/Results because in its present form it may be confusing for the reader: which color means what.

We thank the reviewer for this helpful request for clarification. We agree that the previous wording may have caused confusion regarding the meaning of different MCNP colors. Accordingly, we have revised the Methods section and the relevant figure legends to clearly state that the color assignment of MCNP dyes is not fixed across different experiments or figures. The use of different colors serves solely for visualization and presentation purposes, facilitating the distinction of anatomical structures in multichannel and three-dimensional imaging, and does not indicate any fixed or intrinsic correspondence between a specific color and a particular vascular or ductal system. We believe that this clarification will help prevent misinterpretation and improve the overall clarity of the manuscript.

(17) Still I think the hepatic artery is extremely shrunk, while the portal vein is extremely dilated. Please, note that in the referring figure (from Adori et al), hepatic artery and portal vein are ca 50 micrometers and 250 micrometers in diameter, respectively. In your figure, as I see, ca. 9-10 micrometers and 125 micrometers, respectively. This means 5x (Adori) vs. 13-14x differences (you). I would not say that this is necessarily problematic --- but may reflect some perfusion issues that may be good to consider.

We thank the reviewer for the careful comparison and acknowledge the quantitative differences pointed out. Compared with the study by Adori et al., the diameter ratio between the hepatic artery and the portal vein in our images does indeed differ to some extent. We believe that this discrepancy primarily arises from methodological differences in imaging and analysis strategies between the two studies.

In the work by Adori et al., periportal vasculature identification and three-dimensional segmentation were mainly based on 488 nm autofluorescence signals acquired from inverted tissues. This signal predominantly reflects the overall outline of periportal tissue regions rather than direct imaging of the vascular lumen itself. Consequently, the measured “vessel diameter” largely represents a spatial domain delineated by surrounding periportal structures, and does not necessarily correspond to the actual or functional luminal diameter of the vessel.

In contrast, the present study employed fluorescent MCNP dye perfusion under low perfusion pressure, combined with tissue clearing and three-dimensional optical imaging. Under these experimental conditions, the measured vessel diameters more closely reflect the perfusable luminal space of vessels in a fixed state, rather than their maximally dilated diameter, and are not defined by the morphology of surrounding tissues. This distinction is particularly relevant for the hepatic artery: as a high-resistance, smooth muscle–rich vessel, its diameter is highly sensitive to perfusion pressure and post-excision changes in vascular tone. In comparison, the portal vein exhibits greater compliance and is relatively less affected by these factors.

Based on these methodological differences, the observation of relatively smaller apparent hepatic arterial diameters—and consequently a higher arterial-to-portal vein diameter ratio—under dye perfusion–based optical imaging conditions is an expected outcome. Importantly, the primary focus of the present study is the identification and characterization of the periportal lamellar complex (PLC) as a three-dimensional lamellar tissue structure that can be stably and reproducibly recognized across different samples and imaging conditions, rather than absolute comparisons of vascular diameters.

(21) After the presented documentation, I still have some concerns that the 'periportal lamellar complex (PLC)' that the Authors describe is really a distinct anatomical or functional unit. The confocal panel in Fig. 4F is nice and high quality. However, as far as I see, it shows that CD34+/Sca-1+ immunostaining is not specific for the presumptive PLCs in the peri-portal region. Instead, Sca-1 immunoreactivity is highly abundant also in the midzone --- to which the supposed PLCs do not extend, according to the cartoon shown in panel D, same figure. Notably, this questions also the specificity of the single cell analysis.

We thank the reviewer for this detailed and important comment regarding the specificity of CD34⁺/Sca-1⁺ markers and the definition of the periportal lamellar complex (PLC).

It should be emphasized that the PLC is not defined on the basis of any single molecular marker, but rather by a reproducible periportal lamellar anatomical structure consistently revealed by three-dimensional imaging across multiple samples. The co-expression of CD34 and Sca-1 is interpreted within this clearly defined anatomical context and is used to characterize the molecular features of endothelial cells associated with the PLC structure.

As shown in Fig. 4F, the co-expression of CD34 and Sca-1 delineates a continuous, lamellar endothelial structure surrounding the portal vein. In contrast, outside the periportal region—including the midlobular areas—Sca-1 or CD34 expression can also be detected, but these signals appear scattered and discontinuous, lacking an organized lamellar topology.

In the single-cell transcriptomic analysis, we treated CD34⁺/Sca-1⁺ endothelial cells as an operational population to explore molecular features that may be enriched in the microenvironment of the periportal lamellar complex (PLC). Importantly, this analysis was intended to provide molecular clues associated with the PLC, rather than to precisely assign spatial locations or identities to individual cells.

Occasional isolated Sca-1⁺ signals detected outside the periportal region do not affect the anatomical definition of the PLC, nor do they alter the interpretation of the single-cell analysis. These analyses serve to provide supportive and exploratory molecular information for the structural identification of the PLC, rather than constituting decisive spatial evidence.

(23) '....In the manuscript, we have carefully stated that this analysis is exploratory in nature and have avoided overinterpretation. In future studies, high-resolution spatial omics approaches will be invaluable for more precisely delineating the molecular characteristics of these fine structures.'

I do not find these statements either in the Discussion or in the Results. I must reiterate my opinion that the applied methodical approach in the single cell transcriptomics part has severe limitations, and the readers must be aware of this.

We thank the reviewer for this further comment. We understand and acknowledge the reviewer’s concerns regarding the methodological limitations of single-cell transcriptomic analyses, and we agree that these limitations should be clearly communicated to readers in the main text.

We acknowledge that in the previous version of the manuscript, the exploratory nature of the single-cell transcriptomic analysis and its methodological boundaries were discussed only in the response to reviewers and were not explicitly stated in the manuscript itself. We thank the reviewer for pointing out this omission. In the revised manuscript, we have now added explicit clarifications in the main text to prevent potential overinterpretation of these results.

In the present study, our primary effort is focused on the descriptive characterization of the three-dimensional anatomical organization and spatial relationships of the PLC using volumetric imaging and vascular labeling strategies. As a complementary exploratory analysis, we reanalyzed existing liver single-cell transcriptomic datasets to examine endothelial cell populations exhibiting PLC-associated features, and performed differential gene expression and Gene Ontology enrichment analyses. Importantly, these results are intended to provide molecular-level support for the structural identification of the PLC and to offer preliminary insights into its potential biological functions. Accordingly, we have narrowed the presentation and interpretation of the single-cell analysis in both the Results and Discussion sections of the revised manuscript.

In addition, we have expanded the Discussion to address the limitations of current spatial transcriptomic approaches in validating a continuous three-dimensional structure such as the PLC. Most existing spatial transcriptomic methods rely on two-dimensional tissue sections of 8–10 μm thickness, whereas identification of the PLC depends on three-dimensional imaging of tissue volumes with thicknesses of ≥200 μm, making reliable reconstruction of its spatial continuity from single sections challenging. Furthermore, because each spatial transcriptomic capture spot often encompasses multiple adjacent cells, signal mixing effects further limit precise resolution of specific periportal microstructures.

Overall, we agree with the reviewer’s central point that the limitations of single-cell transcriptomic analyses should be clearly understood by readers. By explicitly clarifying the methodological boundaries and refining the related statements in the main text, we believe this concern has now been adequately addressed in the revised manuscript. We thank the reviewer for identifying this omission, which has helped to improve the rigor and clarity of the study.

Reviewer #3 (Recommendations for the authors):

(1) While interesting observations, suitable for discussion, the following sections are speculations, given that no functional characterization of PLC importance has been performed yet. This is the most felt when commenting on the role in hematopoiesis, which transiently takes place in the liver during embryogenesis (Khan et al 2016) but ceases to exist after ligation of the umbilical inlet. Adult Liver hematopoiesis remains controversial, and more solid evidence would need to be presented to support its existence in PLC regions.

265 - These findings suggest that the Periportal Lamellar Complex (PLC) is not only a morphologically and spatially distinct, low-permeability vascular unit surrounding the portal vein, but also likely serves as a critical nexus connecting the portal vein, hepatic artery, and liver sinusoids. Thus, the PLC constitutes a key node within the interactive vascular network of the mouse liver.

We thank the reviewer for the comments and suggestions regarding the potential functional interpretation of the periportal lamellar complex (PLC), particularly its possible association with hematopoietic function. We would like to clarify that the statement on page 265 was intended solely to describe the structural characteristics and spatial organization of the PLC within the periportal vascular network. Specifically, the original wording aimed to summarize the morphological features of the PLC and its spatial relationships among the portal vein, hepatic artery, and hepatic sinusoids.

Nevertheless, to minimize potential misunderstanding, we have revised this section to avoid unnecessary functional implications. The revised text now reads:

“These results suggest that the periportal lamellar complex (PLC) is a morphologically and spatially distinct vascular structure that surrounds the portal vein and may serve as a key organizational node coordinating the spatial relationships among the portal vein, hepatic artery, and hepatic sinusoids. Accordingly, the PLC represents an important structural element within the interactive vascular network of the mouse liver.”

This revision preserves the structural significance of the PLC while avoiding overinterpretation of its functional roles.

(2) The same is true also for this section, following Figure 3 - no functional experiment tested this. For example, diphtheria toxin is expressed in the CD34+Sca1+ population. Or at least a careful mapping of the developing liver, which would indicate if the PLC precedes or follows the BD development.

356 as a spatial positional cue guiding bile duct growth and branching but also as a regulatory node involved in coordinating bile drainage from the hepatic lobule into the biliary network.

To avoid potential misunderstanding, we have further refined and revised the statements in the manuscript regarding the functional interpretation of the periportal lamellar complex (PLC) and its relationship to bile duct development. We agree that cell ablation strategies are of great importance for functional validation studies. However, it should be noted that CD34 and Sca-1 are relatively broadly expressed markers during liver development, labeling multiple endothelial, mesenchymal, and progenitor cell populations, and their expression is not restricted to the PLC. Owing to this broad expression pattern, ablation of CD34⁺Sca-1⁺ cell populations would likely exert widespread effects on vascular and stromal structures, thereby complicating the distinction between direct PLC-specific effects and secondary developmental alterations. As such, this strategy may present technical limitations for specifically dissecting the role of the PLC in bile duct development. At the same time, given that the primary objective of this study is the systematic characterization of the three-dimensional anatomical features and spatial organization of the PLC, we have correspondingly revised the manuscript to restrict statements regarding the relationship between the PLC and bile ducts to spatial associations supported by the current data. Specifically, our results show that primary bile ducts run along the main portal vein trunk, secondary bile ducts exhibit directed branching toward the PLC region, and terminal bile duct branches tend to spatially cluster in the vicinity of the PLC, thereby forming a reproducible periportal spatial arrangement. Based on these observations, the PLC delineates a relatively conserved anatomical microenvironment within the portal region, whose spatial position is closely associated with the organization and terminal distribution of the intrahepatic bile duct network.

We believe that these revisions more accurately reflect the experimental evidence and the defined scope of the present study.

(3) The following statement ought to be rephrased or skipped, considering that CD34 and Sca1 (Ly6a) are markers of periportal endothelial cells (Pietilä et al., 2025, Gómez-Salinero et al., 2022) and as shown by the authors in their own Fig. 6D. In this context and the context of the CCL4 experiments, a "simple" proliferative progenitor portal vein endothelial cell phenotype, suggested also by the presence of DLL4 (Fig5A) and JAG1 (Pietilä et al., 2025) (Benedito et al., 2009) ought to be considered.

409 Notably, CD34 and Sca-1 (Ly6a) were co-expressed exclusively within PLC structures surrounding the portal vein, but absent from central vein ECs and midzonal LSECs (Figure 4F).

We thank the reviewer for pointing out the potential imprecision in this wording. We agree that both CD34 and Sca-1 (Ly6a) are well-established markers of periportal endothelial cells, as previously reported (Pietilä et al., 2025; Gómez-Salinero et al., 2022), and as also illustrated in Fig. 4F of our study.

Accordingly, the original statement suggesting that CD34 and Sca-1 are co-expressed exclusively within the PLC structure may indeed represent an overinterpretation. Following the reviewer’s suggestion, we have revised the relevant text on page 409 by removing the exclusive phrasing (“only in”) and by emphasizing instead that CD34⁺Sca-1⁺ endothelial cells are enriched in periportal regions associated with the PLC, rather than being specific to or confined within the PLC.

In addition, in the context of the CCl₄-induced liver fibrosis model, we agree with the reviewer that the observed expression of DLL4 and JAG1 under fibrotic conditions is more appropriately interpreted as reflecting an activated or proliferative periportal endothelial progenitor–like phenotype, rather than defining a novel endothelial lineage. The corresponding statements in the revised manuscript have been adjusted accordingly.

(4) Again, these concluding sentences are based on correlative evidence of mRNA expression and literature but not experimental evidence.

436 These findings suggest that this unique endothelial cell subset in the periportal region may possess dual regulatory functions in both metabolic and hematopoietic modulation

441 results suggest that PLC endothelial cells may not only regulate periportal microcirculatory blood flow but also help establish a specialized microenvironment that potentially supports periportal hematopoietic regulation, contributing to stem cell recruitment, vascular homeostasis, and tissue repair.

We thank the reviewer for this thoughtful comment. We agree that these statements are primarily based on transcriptomic correlation analyses and support from previous literature, rather than direct functional experimental evidence.

Accordingly, in the revised manuscript, we have appropriately toned down and adjusted the relevant concluding statements to more accurately reflect their inferential nature. The revised wording emphasizes associations and potential involvement, rather than definitive functional roles. These changes preserve the overall scientific interpretation while aligning the level of inference more closely with the available evidence.

The revised text now reads:

“Finally, we found that the main trunk of the PLC is primarily composed of CD34⁺Sca-1⁺CD31⁺ endothelial cells (Fig. 4J). These CD34⁺Sca-1⁺ double-positive cells are mainly distributed in the basal region of the PLC structure and exhibit molecular features associated with hematopoiesis. Taken together, these results suggest that PLC endothelial cells may contribute to the establishment of a local microenvironment related to periportal hematopoietic regulation and may play potential roles in stem cell recruitment and maintenance of vascular homeostasis.”

(5) The following part is speculative and based on re-analysis from the dataset that was gathered after 6 more weeks of CCL4 treatment (12weeks Su et al., 2021), then in the linked experiments from the manuscript. And should be moved to discussion or removed.

504 Moreover, single-cell transcriptomic re-analysis revealed significant upregulation of bile duct-related genes in the CD34⁺Sca-1⁺ endothelium of PLC in fibrotic liver, with notably high expression of Lgals1 (Galectin-1) and Hgf (Figure 5G). Previous studies have shown that Galectin-1 is absent in normal liver parenchyma but highly expressed in intrahepatic cholangiocarcinoma (ICC), correlating with tumor dedifferentiation and invasion (Bacigalupo, Manzi, Rabinovich, & Troncoso, 2013; Shimonishi et al., 2001). Additionally, hepatocyte growth factor (HGF), particularly in combination with epidermal growth factor (EGF) in 3D cultures, promotes hepatic progenitor cells to form bile duct-polarized cystic structures (N. Tanimizu, Miyajima, & Mostov, 2007). Together, these findings suggest the PLC endothelium may act as a key regulator of bile duct branching and fibrotic microenvironment remodeling in liver fibrosis.

Collectively, our results demonstrate that the PLC, situated between the portal vein and periportal sinusoidal endothelium, constitutes a critical vascular microenvironmental unit. It may not only colocalize with bile duct branches under normal physiological conditions, but also through its basal CD34⁺Sca-1⁺ double-positive endothelial cells, potentially orchestrate bile duct epithelial proliferation, branching morphogenesis, and bile acid transport homeostasis via multiple signaling pathways. Particularly during liver fibrosis progression, the PLC exhibits dynamic structural extension, serving as a spatial scaffold facilitating terminal bile duct migration and expansion into the hepatic parenchyma (Figure 5H). These findings highlight the PLC endothelial cell population and the vascular-bile duct interface as key regulatory hubs in bile duct regeneration, tissue repair, and pathological remodeling, providing novel cellular and molecular insights for understanding bile duct-related diseases such as ductular reaction, cholangiocarcinoma, and cholestatic disorders, and offering potential targets for therapeutic intervention.

We thank the reviewer for this careful and thought-provoking comment. We understand and agree with the reviewer’s assessment that this section involves a degree of inference, as the analysis is based on a re-analysis of a previously published single-cell transcriptomic dataset from a CCl₄-induced liver fibrosis model (Su et al., 2021), rather than on experimental data directly generated in the present study.

In response to the reviewer’s suggestion, we have carefully re-examined and revised the relevant paragraphs. Without altering the overall structure of the manuscript, we have appropriately moderated the wording to clarify that these results primarily describe the transcriptional features of PLC-associated CD34⁺Sca-1⁺ endothelial cells under fibrotic conditions, and their associations with bile duct–related gene expression, rather than providing direct functional evidence for their roles in bile duct branching or microenvironmental remodeling.

In addition, we have explicitly clarified in the main text the data source and methodological limitations of the single-cell transcriptomic analysis, and emphasized that these findings should be interpreted in conjunction with the spatial information revealed by three-dimensional imaging. Through these revisions, we aim to retain the value of this analysis in providing complementary molecular insight into PLC characteristics, while avoiding potential over-interpretation of its functional implications.

Formal suggestions:

(6) The following sentence would benefit from being more clearly written.

263 - The formation of PLC structures in the adventitial layer may participate in local blood flow regulation, maintenance of microenvironmental homeostasis.

We thank the reviewer for this helpful suggestion. The sentence has been revised to improve clarity by correcting the parallel structure and refining the wording.

The formation of PLC structures in the adventitial layer may participate in local blood flow regulation and the maintenance of microenvironmental homeostasis.

(7) The following sentence is misleading as it implies cell sorting, and "subsetted" rather than "sorted" should be used.

414 Based on this, we sorted CD34⁺Sca-1⁺ endothelial populations from the total liver EC pool (Figure 4G).

Thank you for your comment.

We have revised the term as suggested. This avoids the misleading implication of physical sorting, as our operation was analytical subsetting of the target subpopulation.

We appreciate your careful review.

(8) Correct typos, especially in the results section related to Fig. 6. and formatting issues in the discussion.

730 Morphologically, the PLC shares features with previously described telocytes (TCs)- 731 a recently identified class of interstitial cells in the liver observed via transmission electron

We thank the reviewer for pointing out this textual error. In the submitted version, the sentence describing the morphological similarity between the PLC and previously reported telocytes was inadvertently interrupted due to a punctuation issue. This has now been corrected to ensure sentence integrity and consistent formatting.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study by Xu et al. focuses on the impact of clathrin-independent endocytosis in cancer cells on T cell activation. In particular, by using a combination of biochemical approaches and imaging, the authors identify ICAM1, the ligand for T cell-expressed integrin LFA-1, as a novel cargo for EndoA3-mediated endocytosis. Subsequently, the authors aim to identify functional implications for T cell activation, using a combination of cytokine assays and imaging experiments.

They find that the absence of EndoA3 leads to a reduction in T cell-produced cytokine levels. Additionally, they observe slightly reduced levels of ICAM1 at the immunological synapse and an enlarged contact area between T cells and cancer cells. Taken together, the authors propose a mechanism where EndoA3-mediated endocytosis of ICAM1, followed by retrograde transport, supplies the immunological synapse with ICAM1. In the absence of EndoA3, T cells attempt to compensate for suboptimal ICAM1 levels at the synapse by enlarging their contact area, which proves insufficient and leads to lower levels of T cell activation.

Strengths:

The authors utilize a rigorous and innovative experimental approach that convincingly identifies ICAM1 as a novel cargo for Endo3A-mediated endocytosis.

Weaknesses:

The characterization of the effects of Endo3A absence on T cell activation appears incomplete. Key aspects, such as surface marker upregulation, T cell proliferation, integrin signalling and most importantly, the killing of cancer cells, are not comprehensively investigated.

We agree with the reviewer that the effects of EndoA3 depletion on T cell activation were not characterized enough. In new data presented in Fig.S4G-J, we explored additional activation markers and proliferation parameters. We didn’t observe any difference for the surface markers PD-1, CD137 and Tim-3 between LB33-MEL EndoA3+ cells treated with control and EndoA3 siRNAs. Regarding proliferation (Fig. S4J), although the proliferation index seems slightly lower upon EndoA3 depletion, we didn’t observe any significant difference either. Degranulation has also been monitored (Fig. S4K), but we didn’t observe any significant differences. In the new Fig. 3F however, we performed chromium release assays to assess the killing of cancer cells. Very interestingly, we observed an ~15% higher lysis of LB33-MEL EndoA3+ cells after EndoA3 depletion, when compared to the control condition at a ratio of 3:1 T cells:target cells (where the maximal effect is observed). These data are further discussed in the discussion section (new §6-9).

As Endo- and exocytosis are intricately linked with the biophysical properties of the cellular membrane (e.g. membrane tension), which can significantly impact T-cell activation and cytotoxicity, the authors should address this possibility and ideally address it experimentally to some degree.

Evaluating changes in the biophysical properties of cancer cell plasma membrane upon EndoA3 depletion is not trivial. An indirect way to address this question is by observing the area and shape of cells after siRNA treatment. In the new data added in the new Fig. S4B-D, we compared the area, aspect ratio and roundness of LB33-MEL EndoA3+ cells treated with negative control or EndoA3 siRNAs. While we observed a slight cell area reduction upon EndoA3 depletion, no significant changes were observed regarding the aspect ratio and the roundness. Hence, we think that the biophysical properties of cancer cells are not drastically modified by EndoA3 depletion.

Crucially, key literature relevant to this research, addressing the role of ICAM1 endocytosis in antigen-presenting cells, has not been taken into consideration.

We thank the reviewer for this important point. We have now considered and cited the relevant literature (Discussion, Page no.9).

Reviewer #2 (Public review):

Summary:

The manuscript by Xu et al. studies the relevance of endophilin A3-dependent endocytosis and retrograde transport of immune synapse components and in the activation of cytotoxic CD8 T cells. First, the authors show that ICAM1 and ALCAM, known components of immune synapses, are endocytosed via endoA3-dependent endocytosis and retrogradely transported to the Golgi. The authors then show that blocking internalization or retrograde trafficking reduces the activation of CD8 T cells. Moreover, this diminished CD8 T cell activation resulted in the formation of an enlarged immune synapse with reduced ICAM1 recruitment.

Strengths:

The authors show a novel EndoA3-dependent endocytic cargo and provide strong evidence linking EndoA3 endocytosis to the retrograde transport of ALCAM and ICAM1.

Weaknesses:

The role of EndoA3 in the process of T cell activation is shown in a cell that requires exogenous expression of this gene. Moreover, the authors claim that their findings are important for polarized redistribution of cargoes, but failed to show convincingly that the cargoes they are studying are polarized in their experimental system. The statistics of the manuscript also require some refinement.

We fully acknowledge that the requirement for exogenous expression of EndoA3 in our immunological model represents a limitation of our study. Unfortunately, it remains challenging to identify cancer cell lines for which autologous CD8 T cells are available and that endogenously express all molecular players investigated (in particular EndoA3). At this stage, we do not have access to any other cancer cell line/autologous CD8⁺ T cell pairs that are sufficiently well characterized. In future studies, it would be valuable to investigate tumor types with high endogenous EndoA3 expression (such as glioblastomas, gliomas, and head and neck cancers) for which autologous CD8 T cells could be obtained, but this remains technically challenging.

To address the reviewer’s second point regarding polarized redistribution of cargoes, we have added new data in the new Figure 4 and Movies S8-9. Using high-speed spinningdisk live-cell confocal microscopy, we captured the movement of ICAM1-positive tubulovesicular carriers in cancer cells at the moment of contact with CD8 T cells. Capturing such events is technically challenging, as T cell–cancer cell contacts form randomly and transiently. Successful imaging requires that the cancer cell be well spread and express ICAM1–GFP at an optimal level (as it is transiently expressed as a GFP-tagged construct), while acquisition must occur precisely at the moment when the T cell initiates contact. Despite these technical constraints, we successfully imaged early stages of immune synapse formation, enabling visualization of ICAM1 vesicular transport.

The data reveal a flux of ICAM1-positive carriers emerging from the perinuclear region (corresponding to the Golgi area) and moving toward the contact site with the CD8 T cell, with fusion events of vesicles occurring at the developing immune synapse. AI-based segmentation and tracking analyses showed that ICAM1-positive carrier trajectories were predominantly oriented toward the forming immune synapse, whereas carriers moving toward other cellular regions were markedly less frequent. These results provide direct evidence for polarized ICAM1 transport via vesicular trafficking toward the immune synapse.

Reviewer #3 (Public review):

Summary:

Shiqiang Xu and colleagues have examined the importance of ICAM-1 and ALCAM internalization and retrograde transport in cancer cells on the formation of a polarized immunological synapse with cytotoxic CD8+ T cells. They find that internalization is mediated by Endophilin A3 (EndoA3) while retrograde transport to the Golgi apparatus is mediated by the retromer complex. The paper is building on previous findings from corresponding author Henri-François Renard showing that ALCAM is an EndoA3dependent cargo in clathrin-independent endocytosis.

Strengths:

The work is interesting as it describes a novel mechanism by which cancer cells might influence CD8+ T cell activation and immunological synapse formation, and the authors have used a variety of cell biology and immunology methods to study this. However, there are some aspects of the paper that should be addressed more thoroughly to substantiate the conclusions made by the authors.

Weaknesses:

In Figure 2A-B, the authors show micrographs from live TIRF movies of HeLa and LB33MEL cells stably expressing EndoA3-GFP and transiently expressing ICAM-1-mScarlet. The ICAM-1 signal appears diffuse across the plasma membrane while the EndoA3 signal is partially punctate and partially lining the edge of membrane patches. Previous studies of EndoA3-mediated endocytosis have indicated that this can be observed as transient cargo-enriched puncta on the cell surface. In the present study, there is only one example of such an ICAM-1 and EndoA3 positive punctate event. Other examples of overlapping signals between ICAM-1 and EndoA3 are shown, but these either show retracting ICAM1 positive membrane protrusions or large membrane patches encircled by EndoA3. While these might represent different modes of EndoA3-mediated ICAM-1 internalization, any conclusion on this would require further investigation.

We agree with the reviewer that the pattern of cargoes during endocytosis (puncta vs large patches) as observed by live-cell TIRF microscopy may be confusing. Actually, a punctate pattern has been observed quasi systematically when we monitored the uptake of endogenous cargoes via antibody uptake assays (whatever the imaging approach: TIRF, spinning-disk, classical confocal or lattice light-sheet microscopy). For example:

- ALCAM: Fig.1e-h, Supplementary Figure 5 and Supplementary Movies 1-3 and 6 in Renard et al. 2020, https://doi.org/10.1038/s41467-020-15303-y; Fig.1D and Movie 2 in Tyckaert et al. 2022, https://doi.org/10.1242/jcs.259623.

- L1CAM: Fig.2 and 3D, Movies S1-4 in Lemaigre et al. 2023, https://doi.org/10.1111/tra.12883.

In rare examples, bigger clusters of antibodies were observed, where EndoA3 was observed to surround them, delineate them in a “lasso-like” pattern, and the clusters were progressively taken up:

- ALCAM: Supplementary Movie 4 in Renard et al. 2020, https://doi.org/10.1038/s41467-020-15303-y.

However, bigger patches of cargoes were more often observed when uptake was observed using transient expression of GFP-/mCherry-tagged versions of cargoes. In these cases, EndoA3 was predominantly observed to delineate cargo patches as a “lasso-like” pattern, progressively triming those patches leading to endocytosis. For example:

- L1CAM: Fig.3E, Movie S5-7 in Lemaigre et al. 2023, https://doi.org/10.1111/tra.12883.

- We also observed this pattern with CD166-GFP (unpublished).

The fact that we observed rather patches than punctate patterns upon transient expression of fluorescently-tagged constructs of cargoes is likely due to the elevated expression level of the cargoes.

Therefore, the patchy pattern observed for ICAM1 and ALCAM, transiently expressed in fusion with fluorescent proteins, and surrounded by EndoA3 in Fig.2A-B and old Movies S1-3, is not surprising. Of note, upon anti-ALCAM antibody uptake, we observed a more punctate pattern (Fig.2C), as previously described. Unfortunately, the lower quality of commercial anti-ICAM1 antibody did not allow us to proceed to uptake assays as for ALCAM.

Regarding Fig.S2 and old Movies S4-5, we agree with the reviewer that these data may be misleading, as they represent phenomena happening at protrusions and contact zones between two adjacent cells. We have now replaced these images with other examples where we avoid contact zones (Fig.S2 and new Movies S5-7).

These different patterns (patches vs dots) are still unexplained at the current stage, and may indeed represent different modes of endocytosis. We think these various patterns may depend on the abundance/expression level of cargoes and their degree of clustering. This will be investigated in future studies. Still, whatever the pattern, these data demonstrate and confirm the association between EndoA3 and cargoes (such as ICAM1 or ALCAM), even in the absence of antibodies.

Moreover, in Figure 2C-E, uptake of the previously established EndoA3 endocytic cargo ALCAM is analyzed by quantifying total internal fluorescence in LB33-MEL cells of antibody labelled ALCAM following both overexpression and siRNA-mediated knockdown of EndoA3, showing increased and decreased uptake respectively. Why has not the same quantification been done for the proposed novel EndoA3 endocytic cargo ICAM-1? Furthermore, if endocytosis of ICAM-1 and ALCAM is diminished following EndoA3 knockdown, the expression level on the cell surface would presumably increase accordingly. This has been shown for ALCAM previously and should also be quantified for ICAM-1.

As correctly pointed by the reviewer, anti-ICAM1 antibody uptake assays would have been great. We have tried to do them many times. Unfortunately, all commercial antibodies we tested did not yield satisfying results in uptake experiments. Either the labeling was too week/non-specific, or the antibody was not effectively stripped from the cell surface by acid washes, i.e. the acid-wash conditions required for efficient stripping were too harsh for the cells to tolerate. We have tried other approaches using the same commercial antibody which do not require acid washes (loss of surface assays by FACS, or uptake assays using surface protein biotinylation) or based on insertion of an Alfa-tag in the extracellular part of ICAM1 by CRISPR-Cas9 and detection of ICAM1 with an antiAlfa-tag nanobody (unpublished approach; collaboration with the lab of Prof. Leonardo Almeida-Souza, University of Helsinki, who developed the approach), but without success. However, we were more successful with the SNAP-tag-based approach to follow retrograde transport, for which the commercial anti-ICAM1 antibody worked properly. In Fig. 1F, we could show that retrograde transport of ICAM1 (and thus most likely its endocytosis step) was significantly decreased upon EndoA3 depletion in HeLa cells, indirectly demonstrating that ICAM1 is effectively an EndoA3-dependent cargo.

Regarding the fact that surface level of ICAM1 should increase upon perturbation of EndoA3-mediated endocytosis, we agree with the reviewer that this could be an expected result. However, this is not necessarily systematic, as the surface level of a protein cargo is always the result of a balance between its endocytosis, recycling to plasma membrane, and lysosomal degradation. We also have to take into account the neosynthesized protein flux. One must also consider that multiple endocytic mechanisms exist in parallel, and that the perturbation of one mechanism (EndoA3-mediated CIE, here) may be partially compensated by others, as cargoes can often be taken up via multiple endocytic doors. Hence, an increased abundance at the cell surface is not always guaranteed upon endocytosis perturbation. Anyway, we measured the cell surface level of both ICAM1 and ALCAM in LB33-MEL EndoA3+ cells treated with negative control or EndoA3 siRNAs (Fig. S4E-F). Only minor differences were observed.

In Figure 4A the authors show micrographs from a live-cell Airyscan movie (Movie S6) of a CD8+ T cell incubated with HeLa cells stably expressing HLA-A*68012 and transiently expressing ICAM1-EGFP. From the movie, it seems that some ICAM-1 positive vesicles in one of the HeLa cells are moving towards the T cell. However, it does not appear like the T cell has formed a stable immunological synapse but rather perhaps a motile kinapse. Furthermore, to conclude that the ICAM-1 positive vesicles are transported toward the T cell in a polarized manner, vesicles from multiple cells should be tracked and their overall directionality should be analyzed. It would also strengthen the paper if the authors could show additional evidence for polarization of the cancer cells in response to T-cell interaction.

A similar point was raised by reviewer #2. We have revised this section accordingly. In the new Fig. 4 and Movies S8-9, we replaced the live-cell Airyscan confocal data with highspeed spinning-disk confocal imaging data, enabling a more accurate analysis of cargo polarized redistribution and at a higher time resolution.

Using this approach, we captured the movement of ICAM1-positive tubulo-vesicular carriers in cancer cells at the moment of contact with CD8 T cells. Capturing such events is technically challenging, as T cell–cancer cell contacts form randomly and transiently. Successful imaging requires that the cancer cell be well spread and express ICAM1–GFP at an optimal level (as it is transiently expressed as a GFP-tagged construct), while acquisition must occur precisely at the moment when the T cell initiates contact. Despite these technical constraints, we successfully imaged early stages of immune synapse formation, enabling visualization of ICAM1 vesicular transport.

The data reveal a flux of ICAM1-positive carriers emerging from the perinuclear region (corresponding to the Golgi area) and moving toward the contact site with the CD8 T cell, with fusion events of carriers occurring at the developing immune synapse.

AI-based segmentation and tracking analyses showed that ICAM1-positive carrier trajectories were predominantly oriented toward the forming immune synapse, whereas carriers moving toward other cellular regions were markedly less frequent. These results provide direct evidence for polarized ICAM1 transport via vesicular trafficking toward the immune synapse.

Finally, in Figures 4D-G, the authors show that the contact area between CD8+ T cells and LB33-MEL cells is increased in response to siRNA-mediated knockdown of EndoA3 and VPS26A. While this could be caused by reduced polarized delivery of ICAM-1 and ALCAM to the interface between the cells, it could also be caused by other factors such as increased cell surface expression of these proteins due to diminished endocytosis, and/or morphological changes in the cancer cells resulting from disrupted membrane traffic. More experimental evidence is needed to support the working model in Figure 4H.

Regarding the cell surface expression of both ICAM1 and ALCAM, as already explained above, only minor differences were observed (Fig. S4E-F). Regarding morphological changes of cancer cells upon EndoA3 depletion (Fig. S4B-D), we compared the area, aspect ratio and roundness of LB33-MEL EndoA3+ cells treated with negative control or EndoA3 siRNAs. While we observed a slight cell area reduction upon EndoA3 depletion, no significant changes were observed regarding the aspect ratio and the roundness. Cancer cell morphology is thus not drastically modified by EndoA3 depletion. All these new data are now discussed in the manuscript.

Recommendations for the authors:

Reviewing Editor Comments:

The reviewers discussed the paper and all agreed it was incomplete in supporting the conclusions. Additional data needed to support the conclusions were:

(1) Better characterisation of Endo3A-expressing and knock-down cells such as morphology, ICAM-1, and ALCAM surface levels to name two parameters.

As discussed above, we have now added new data addressing these points:

- Morphology: Fig. S4B-D

- ICAM1 and ALCAM surface levels: Fig. S4E-F These new data are discussed in the main text.

(2) Better characterisation of the ICAM-1 polarisation process. Does this require interaction with LFA-1 can ICAM-1 be delivered to the synapse without this?

As discussed above, we have now added new data better addressing the characterization of ICAM1 polarized trafficking to the immune synapse, that can be found in the new Fig. 4 (high-speed spinning-disk confocal imaging of ICAM1 trafficking upon conjugate formation between CD8 T cell and cancer cell). The text has been modified accordingly. The dependency on LFA-1 has not been addressed directly, but we may suppose it is indeed important as (i) it has already been addressed in other cellular systems by previous studies (Jo et al. 2010), and (ii) we observed a denser flux of ICAM1-positive carriers in the cancer cell toward regions involved in immune synapses with CD8 T cells, than other regions. As we didn’t address this question more directly in our study, we briefly mentioned this point in the Discussion section.

(3) Better characterisation of T cell response- activation markers, cytotoxicity assays.

As discussed above, we have now added new data addressing these points:

- Cell surface activation markers: Fig. S4G-I

- Proliferation: Fig. S4J

- Degranulation: Fig. S4K

- Cytotoxic activity: Fig. 3F

These new data are discussed in the main text.

(4) Citing relevant literature.

The relevant literature (in particular the paper by Jo et al. 2010) is now cited and discussed.

(5) Number of donors evaluated - is it true there was only one blood donor? For human studies better to have key results on >4 donors.

Our immunological working model indeed originates from a single patient (Baurain et al., 2000), from whom both a cancer cell line (LB33-MEL) and autologous CD8 T cells were derived. These CD8 T cells specifically recognize an HLA molecule presenting a defined antigenic peptide (MUM-3) on the surface of the cancer cells. This provides us with a unique and fully natural experimental system that allows us to faithfully reconstitute cytotoxic T lymphocyte (CTL)-mediated killing of cancer cells in vitro.

Using CD8 T cells from other donors would not be meaningful in this context, as they would not recognize the LB33-MEL cells. Conversely, testing the same CD8 T cells on other cancer cell lines requires engineering these lines to express the appropriate HLA molecule and to be exogenously pulsed with the correct antigenic peptide – which is precisely what we did with the HeLa cell line.

Therefore, increasing the number of donors would require obtaining both cancer cell lines and CD8 T cells from each donor, ideally with evidence that the donor’s T cells recognize their own tumor cells. This is technically challenging and not trivial, although it would indeed be highly valuable to diversify immunological models in future studies.

Importantly, the high specificity of our autologous co-culture system, where cancer cells interact with their naturally matched CD8 T cells, offers clear advantages over commonly used in vitro models such as Jurkat (T) and Raji (B) cell lines, which rely on artificial stimulation with a superantigen to enforce immunological synapse formation and T cell activation.

(6) How does the binding of antibodies to ICAM-1 and ALCAM impact their trafficking?

As IgG antibodies are bivalent and can bind two target antigens, they may induce clustering, which could in turn affect endocytosis. To address this concern, we performed an uptake assay based on surface protein biotinylation using a cleavable biotin reagent (with a reducible linker). Briefly, after allowing endocytosis for different time intervals, cell surface–exposed biotins were removed by treatment with the cellimpermeable reducing agent MESNA, while internalized (endocytosed) biotinylated proteins remained protected. These internalized proteins were then recovered by affinity purification on streptavidin resin and analyzed by Western blot to detect the protein of interest.

Importantly, this uptake assay can be performed in the absence or presence of an anticargo antibody, allowing assessment of its potential influence on endocytosis. Author response image 1 shows the results for ALCAM uptake in HeLa cells, with and without anti-ALCAM antibody:

Author response image 1.

Antibody binding to an extracellular epitope of ALCAM increases its endocytosis. HeLa cellsurface proteins were biotinylated on ice using EZ-Link Sulfo-NHS-SS-Biotin (Pierce) and then incubated at 37 °C for the indicated times to allow endocytosis. Internalization was assessed in the absence or presence of an anti-ALCAM antibody (Ab) added to the extracellular medium. Endocytosis was stopped by returning the cells to ice, and surface-exposed biotin was removed by treatment with the cell-impermeable reducing agent MESNA. Internalized, MESNA-resistant biotinylated proteins were affinity-purified on streptavidin resin and analyzed by Western blot to detect ALCAM. The “unstripped” condition shows the total amount of ALCAM at the cell surface at the beginning of the experiment (signal at ~95 kDa). Quantification of the time course (normalized to the no-antibody condition) shows increased ALCAM endocytosis in the presence of antibody at 15 and 30 min. Blot is representative of two independent experiments; quantifications include data from both experiments.

We observed that the anti-ALCAM antibody slightly enhanced ALCAM uptake. A similar experiment was attempted for ICAM1, but we were unable to detect the protein by Western blot using the available commercial antibody.

Although this outcome was expected, it highlights a potential caveat in using antibodies to monitor endocytosis. Alternative tools such as nanobodies, while monovalent and theoretically less perturbing, are not yet available for many cargo proteins and may still influence cargo conformation or dynamics. Therefore, antibodies remain the current gold standard in endocytosis studies. Nevertheless, data obtained with antibodies should always be validated by complementary approaches that do not rely on antibody binding, as we have done in this study (e.g. live-cell imaging of fluorescently tagged proteins).

The work is of interest and we look forward to your response/revision.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Thank you for submitting your manuscript which I had the pleasure to review. While I enjoyed your work, I feel that it would strongly benefit by addressing the following points:

(1) In-depth characterization of T cell responses upon Endo3A depletion: The characterization should be expanded to include surface marker upregulation, T cell proliferation, and, most importantly, tumor cell cytotoxicity. I was wondering if the incomplete characterization of T-cell responses is due to limited supplies of antigenspecific T-cells? My understanding is that these cells have been derived from a single patient. This also raises concerns in terms of reproducibility as all data are practically from a single biological replicate. My suggestion would be to use an additional system of specific cell-cell contacts to complement the current findings. For instance, HeLa cells could be transfected to express CD19 or EpCAM, for both of which bispecific T cell engagers (Invivogen) exist that would allow specific contact formation, thereby allowing the study of the effect of Endo3A depletion across T cells from different donors and through a more complete set of assays.

We refer the reviewer to our responses above, where these points have been addressed in detail. We sincerely thank the reviewer for the excellent suggestion of transfecting HeLa cells with CD19 or EpCAM and using bispecific T-cell engagers. However, after careful consideration, we concluded that this approach falls outside the scope of the present study, which was specifically designed to investigate the most natural system, cancer cells and their autologous CD8 T cells. We nevertheless appreciate this insightful suggestion and will certainly consider it for future studies.

(2) Alterations in membrane tension as an alternative explanation: Endo- and exocytosis have been found to influence the biophysical properties of cells, such as membrane tension (e.g., Djakbaravo et al., 2021, PMID: 33788963), which in turn influences their susceptibility to cytotoxic T cells with lower tension corresponding to reduced cytotoxicity (e.g., Basu & Whitlock, 2016, PMID: 26924577). Thus, interference with endocytic pathways could arguably lead to changes in membrane tension that could contribute to the observed effects. These possible effects should be discussed and addressed experimentally to a degree. While measuring membrane tension directly requires specialized expertise (e.g., tether pulling experiments) and is not within the scope of this study, membrane tension affects cell spreading and actin organization. Thus, I would suggest conducting a thorough comparative phenotypical and morphological characterization of the Endo3A+ and Endo3A- cancer cells to estimate the possible effect of changes in membrane tension (if any) on the results.

We refer the reviewer to our responses above, where these points have been addressed in detail. New data have been added and the text of our manuscript has been modified accordingly.

(3) Citation and consideration of earlier work: Jo & Kwon et al., 2010 (PMID: 20681010) have previously shown that ICAM1 undergoes clathrin-independent recycling and repolarization to the immunological synapse in APCs. Furthermore, they provided evidence that actin-based transport, but not lateral diffusion, together with recycling is crucial for the repolarization of ICAM1 to the immunological synapse. This important earlier work has to be cited. Actin-based transport on the cell surface has not been considered in the current manuscript. In light of these earlier findings, it is unclear in Figure 4A if ICAM1 is delivered to the T cell from within- or from the surface of the cancer cell. I would suggest changing the imaging modalities in this experiment to be able to differentiate cell surface from internal ICAM1, e.g., by detaching the cancer cells from the surface as has been done in Fig. 4B, E, and F.

We refer the reviewer to our responses above, where these points have been addressed in detail. New data have been added and the text of our manuscript has been modified accordingly.

Reviewer #2 (Recommendations for the authors):

Major comments:

(1) The authors should be more careful with their claims about the importance of their results for cell polarity as their evidence for this is scarce (i.e. The live-cell imaging in Figure 4A is not quantified and the ICAM1 polarization effect shown in figure 4B-C is, albeit significant, small and not very convincing).

We refer the reviewer to our responses above, where these points have been addressed in detail. New data have been added and the text of our manuscript has been modified accordingly.

(2) The absence (or very low expression) of EndoA3 on the LB33-MEL cell suggests that EndoA3-mediated recycling of immune synaptic components is not required for T-cell activation. The fact that EndoA3 exogenous expression in LB33-MEL cells leads to increased cytokine production in T cells is, however, interesting.

We fully agree with the reviewer’s observation. Although EndoA3 is not expressed in some cellular contexts, its cargoes may still be present. It is therefore reasonable to assume that alternative endocytic mechanisms can compensate for its absence. It is now widely accepted that many cargoes can be internalized through multiple endocytic routes, and that the relative contribution of each pathway depends strongly on the cellular and physiological context.

For example, we have shown that ALCAM and L1CAM, although primarily internalized via clathrin-independent pathways, present a minor fraction (< 25%) undergoing clathrinmediated endocytosis (Renard et al., 2020; Lemaigre et al., 2023). Moreover, we observed that inhibition of macropinocytosis enhances EndoA3-mediated endocytosis of ALCAM, indicating a crosstalk between specific EndoA3-mediated clathrin-independent endocytosis (CIE) and non-specific macropinocytosis (Tyckaert et al., 2022).

Thus, even in the absence of EndoA3, its cargoes are likely internalized through alternative endocytic routes. Nonetheless, our data clearly demonstrate that EndoA3 expression markedly enhances the endocytosis and intracellular trafficking of its cargoes, ultimately leading to modified CD8 T cell responses.

(3) For the statistics in bar graphs (graphs 1C, D, E &F; 3E, 3F, S1C-I, and S3C), one cannot have all values for controls simply normalized to 1. This procedure hides the variance for the controls between each replicate and makes any statistics meaningless.

We thank the reviewer for this important remark. Regarding Figures 1C–F, S1C–I, and S3C, which correspond to quantifications from Western blots, it is standard practice to normalize the quantification to a control condition set to 1 (or 100%). Absolute signal intensities cannot be directly compared across different blots due to the variability inherent to this semi-quantitative technique. For this reason, we chose to keep the data presented in normalized form. However, we agree that this type of data require the careful choice of a convenient statistical analysis approach. Here, we choose one-sample T tests, allowing to test the hypothesis that the various siRNA conditions are different from 100% (the normalized value of the siCtrl condition). We adapted the statistical analysis accordingly in the different figures mentioned.

Regarding old Figures 3E–F (now Fig. 3E and 3G), which correspond to IFNγ secretion assays, we agree that representing IFNγ secretion as a fold change relative to a control condition may obscure inter-experimental variability. However, this format was intentionally chosen to facilitate data interpretation, as IFNγ secretion was quantified by ELISA and also displayed inter-experimental variability. For completeness, we now provide below the corresponding graphs showing absolute IFNγ concentrations, which retain the information on inter-experimental variability (Author response image 2). As you can see, the overall conclusions remain unchanged.

Author response image 2.

IFNg secretion data corresponding to Fig. 3E and 3G, expressed in absolute values (pg/mL)

Minor comments:

(1) What happens to surface and total levels of ICAM1 and ALCAM in the retromer or EndoA3 knockdown/overexpression conditions? This information would put the effects described into context.

We refer the reviewer to our responses above, where these points have been addressed in detail. New data have been added and the text of our manuscript has been modified accordingly.

(2) The authors should clearly indicate that BFA means bafilomycin A in the figure legend or methods.

BFA corresponds to Brefeldin A. We have now clarified this information in legends and methods.

(3) In the sentence: "These data demonstrate that retromer-mediated retrograde transport is critical for trafficking ALCAM and ICAM1 to the Golgi and that this process requires the full secretory capacity of the TGN." What do the authors mean by full secretory capacity?

We have modified the sentence: “Together, these data demonstrate that retromermediated retrograde transport is critical for trafficking ALCAM and ICAM1 to the Golgi and that this process requires efficient secretion from the TGN (as evidenced by the involvement of Rab6).”

(4) The method used for retrograde transport seems to be a variation of the original protocol (reference 43). The manuscript would benefit from a thorough explanation of this assay, rather than citing the original protocol.

We did not modify the original SNAP-tag–based protocol used to monitor retrograde transport. A comprehensive methodological paper has been published (ref. 44), and we have followed it strictly. Additionally, we briefly summarized the rationale of the approach in Figure 1A and in the first paragraph of the Results section.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In their manuscript, Richter and colleagues comprehensively investigate the cell wall recycling pathway in the model alphaproteobacterium Caulobacter crescentus using biochemical, imaging, and genetic approaches. They clearly demonstrate that this organism encodes a functional peptidoglycan recycling pathway and demonstrate the activities of many enzymes and transporters within this pathway. They leverage imaging and growth assays to demonstrate that mutants in peptidoglycan recycling have varying degrees of beta-lactam sensitivity as well as morphological and cell division defects. They propose that, rather than impacting the levels or activity of the major beta-lactamase, BlaA, defects in PG recycling lead to beta-lactam sensitivity by limiting the availability of new cell wall precursors. The findings will be of interest to those in the field of bacterial cell wall biochemistry, antibiotics and antibiotic resistance, and bacterial morphogenesis.

Strengths:

Overall, the manuscript is laid out logically, and the data are comprehensive, quantitative, and rigorous. The mutants and their phenotypes will be a valuable resource for Caulobacter researchers.

Thank you for this positive evaluation. Previous work has mostly focused on the role of PG recycling in the regulation of ampC expression. However, our study and recent work in A. tumefaciens (Gilmore & Cava, 2022) and C. crescentus (Modi et al, 2025) demonstrates that β-lactam resistance is heavily influenced by PG recycling and the metabolic state of the cell, even in the presence of high levels of β-lactamase activity. It is likely that these effects are not limited to the two alpha­proteo­bacterial species investigated to date but may be more widely applicable. Therefore, we believe that our results are relevant beyond the Caulobacter field and may help to stimulate similar analyses in other, medi­cally more relevant species.

Weaknesses:

The only major missing piece is the complementation of mutants to demonstrate that loss of the targeted gene is responsible for the observed phenotypes.

In our initial manuscript, we showed that the replacement of the native AmiR and NagZ genes with mutant alleles encoding catalytically inactive variants of the two proteins gave rise to the same pheno­types as gene deletions. This finding indicates that the defects observed were due to the loss of AmiR or NagZ activity, respectively. To rule out artifacts from polar effects, we have now also conducted the requested complementation analysis for the ΔampG, ΔamiR and ΔnagZ mutants. The results obtained show that deletion mutants carrying an ectopically expressed wild-type gene copy behave essentially like the wild-type strain, thereby verify­ing the validity of our conclusions (new Figure 4-figure supple­ment 1).

Reviewer #2 (Public review):

Summary:

Pia Richter et al. investigated the peptidoglycan (PG) recycling metabolism in the alpha-proteobacterium Caulobacter crescentus. The authors first identified a functional recycling pathway in this organism, which is similar to the Pseudomonas route, and they characterized two key enzymes (NagZ, AmiR) of this pathway, showing that AmiR differs in specificity from the AmpD counterpart of E. coli. Further, they studied the effects of deletions within the PG recycling pathway (ampG, amiR, nagZ, sdpA, blaA, nagA1, nagA2, amgK, nagK mutants), showing filamentation and cell widening, thereby revealing a link between PG recycling and cell division. Finally, they provide a link between PG recycling and beta-lactam sensitivity in C. crescents that is not caused by activation of a beta-lactamase, but rather is a result of reduced supply of PG building blocks increasing the sensitivity of penicillin-binding proteins.

Strengths:

This work adds to the understanding of the role of PG recycling in alpha-proteobacteria, which significantly differ in their mode of cell wall growth from the better studied gamma-proteobacteria.

Thank you for pointing out the relevance of our work. As mentioned above, we believe that our work goes beyond understanding the PG recycling pathway in alphaproteobacteria. Importantly, together with previous work, our results demonstrate a so-far largely neglected critical role of PG recycling in β-lactam resistance that goes beyond the mere regula­tion of β-lactamase gene expression. It will be interesting to determine the conservation of this phenomenon among other bacteria and to see whether blocking PG recycling could represent a potential strategy to combat β-lactam resistant pathogens.

Weaknesses:

The findings are not entirely novel as recent studies by Modi et al. 2025 mBio (studying C. crescentus) and Gilmore & Cava 2022 Nat. Commun. (studying Agrobacterium tumefaciens) came to similar conclusions.

Gilmore & Cava have made the seminal finding that blocking anhydro-muropeptide import affects cell wall integrity in a manner that is partly independent of its effect on ampC expression. We now extend this finding by investigating various critical steps in the PG recycling pathway of C. cres­centus, a species lacking an AmpC homolog. Interestingly, by characterizing a variety of different mutants, we show that the morphol­ogical and ampicillin resistance defects they exhibit are not strictly con­nected and vary substantially between strains, suggesting that different steps in PG recycling differ in their importance for cellular fitness and cell wall integrity. This finding suggests that the phenotypes observed are not simply determined by the efficiency of PG recycling but likely result from a combination of factors. Based on the results obtained, we propose a model that highlights the different factors that may be at play and suggests a mechanism explaining their effects on β-lactam resistance and cell division. Our findings partly overlap with the recent study by Modi et al., but there are various points in which we disagree with their findings and conclusions. The need to rigorously validate our differing results led to a signi­ficant delay in the submission of our manuscript.

Reviewer #1 (Recommendations for the authors):

Major Comment

Genetic complementation is lacking for deletion mutants throughout. Could you please provide complemented strains for mutants in key figures where deletion phenotypes are central to the conclusions (e.g., Figure 4 and related supplements).

As explained above, we have not performed the requested comple­mentation experiments and included the data as Figure 4-figure supplement 1.

Other minor comments:

(1) Figure 1

(a) This is a busy schematic; please consider visually separating PG biosynthesis vs. recycling (e.g., a faint divider line or shaded boxes).

We have now simplified the schematic and visually separated the PG recycling and de novo biosyn­thesis pathways.

(b) Please label "Fructose-6-phosphate" and "Glucosamine-6-phosphate (GlcN-6-P)" on the figure, since they are referenced in the caption (line 1410).

The symbols for fructose, glucosamine and phosphate are given in the legend on the right. For consistency, we would therefore prefer not to additionally label these compounds in the figure.

(c) Define all abbreviations in the caption: CM, GTase, TPase; and clarify the legend conventions (e.g., bold vs. regular font; red vs. black text).

The structure of PG and the different lytic enzymes have now been removed from Figure 1. All remaining abbreviations have now been defined in the legend.

(2) Figure 2 - Figure Supplement 2

(a) Panel B: Please include the full chromatogram (it seems to be cropped at 10 min?). For AmiR in particular, it is important to show there are no nearby peaks at earlier retention times (eg GlcNAc).

The region before 10 min is cropped in many published muropeptide profiles because the peaks contained in it are known to correspond to salts, i.e., borate from the reduction step and phos­phate, which are poorly retained on the C18 column (Figure 2–figure supplement 2). As the reviewer stated, free GlcNAc would elute in this region and would not be recognized if it were produced by AmiR. However, AmiR cleaves free anhydro-muropeptides between anhMurNAc and the peptide, and the experiment in Figure 2–figure supplement 2 shows that it does not cleave the bond between MurNAc and peptides in intact peptidoglycan.

(b) Caption line 1439: with AmiR OR the catalytically...

Done.

(3) Figure 3

Panel A: Label the products as NagZ-treated.

In this analysis, we quantify specific intermediates from the total cellular pool of PG recycling inter­mediates. Since the products were not specifically treated with NagZ, we would prefer to keep the figures as it is.

(4) Figure 4 (and Fig. 4-Figure Supplement 1, 2)

(a) Please add complemented strains for ΔampG, ΔamiR, and ΔnagZ under the same conditions.

As described in more detail above, we have now performed the requested complementation analysis.

(b) Figure 4 - Figure S1 - Please include images of all strains quantified in B (e.g. control WT).

Done.

(c) Figure 4 - Figure S2: A. Please include images of all strains quantified in B. Please include spotting dilutions on minimal medium to assess the importance of PG recycling under nutrient limitation, especially given apparent lysis in ΔamiR and ΔampG.

The length distributions of cells grown in PYE medium are taken from Figure 3 and only shown for comparison (as mentioned in the figure legend). To avoid the duplication of images, we would prefer to keep panel A as it is.

We have now performed the requested serial-dilution spot assay on minimal (M2G) medium. The results show that ampicillin resistance de­creases even more dramatically for all strains in this condi­tion. The new data are presented in Figure 4-figure supplement 3C.

(d) Figure 4 - Figures S3: A and B. Please include WT control.

We have now added images of the wild-type strain to panel B of this figure. The serial dilution spot assays shown in panel A were performed on the same plates as those depicted in Figure 4 (as men­tioned in the figure legend). To avoid the duplication of images, we would prefer to keep this panel as it is.

(5) Figure 5

A, C - please include images of WT control.

We have now added images of the wild-type strain to panel A of this figure. The serial dilution spot assays shown in panel C were performed on the same plates as those depicted in Figure 4 (as men­tioned in the figure legend). To avoid the duplication of images, we would prefer to keep this panel as it is.

(6) Figure 6:

(a) A, C - please include images of WT control.

We have now added images of the wild-type strain to panel A of this figure. The serial dilution spot assays shown in panel C were performed on the same plates as those depicted in Figure 4 (as men­tioned in the figure legend). To avoid the duplication of images, we would prefer to keep this panel as it is.

(b) It would be informative to test ΔamgK and ΔanmK on minimal medium (spotting and/or growth curves) to position these steps within the nutrient-dependent fitness landscape.

We have now analyzed the ampicillin sensitivity of the ΔamgK, ΔnagK and ΔamgK ΔnagK strains on minimal medium (see Author response image 1). Consistent with the results obtained for other mutants in the PG recycling pathway, growth on minimal (M2G) medium plates leads to increased ampicillin sensi­tivity of the ΔamgK mutant. By contrast, ΔnagK and, to a lesser extent, ΔamgK ΔnagK cells show an in­creased tolerance to ampicillin under these conditions compared to growth on PYE plates.

This phenomenon may be explained by the strong stimulatory effect of GlcNAc-6-P on NagB acti­vity. In the absence of NagK, GlcNAc-6-P levels drop, leading to reduced activation of NagB1/2. This effect, combined with abundant glucose to support central carbon metabolism may promote the GlcN-6-P biosynthesis through GlmS, thereby increasing the flux of meta­bol­ites into the de novo PG biosynthesis pathway and thus boosting ampicillin tolerance. However, more re­search is required to fully under­stand the molecular basis of this effect. Given that the results are likely to reflect complex interactions bet­ween dysregulated enzyme activity and altered metabolite pools caused by increased glucose avail­ability, they provide only limited insight into the role of PG recycling in ampicillin resistance. We therefore propose excluding this experiment from the present manuscript to avoid confusion.

Author response image 1.

Serial-dilution spot assay investigating the ampicillin resistance of the indicated mutant strains on minimal (M2G) medium plates.

(c) Could Figures 6 and 7 be combined for better comparison and since there is no WT control? If so, could you also include the MurNAc cytoplasmic level quantification for the double mutant (Figure 7)?

We would prefer to keep the two figures separated to avoid creating an overly large figure that contains a total of nine panels. However, we have now included an additional panel in Figure 7 show­ing the levels of MurNAc in the double mutant.

(7) Figure 7. A, C

Please include images of WT control.

We have now added images of the wild-type strain (now panel B). The serial dilution spot assays (now panel D) were performed on the same plates as those depicted in Figure 4 (as men­tioned in the figure legend). To avoid the duplication of images, we would prefer to keep this panel as it is.

(8) Figure 8-S1D, F

Please include images of WT control.

Panel F of this figure already contains a wild-type control.

(9) Figure 10 A, C

Please include images of WT control and ∆amiR (A).

Done.

(10) Figure 11

Consider adding or highlighting in this figure (in a simplified manner) the major PG recycling differences in Caulobacter? The current model doesn't really show any difference that is unknown.

This figure presents a model of the mechanism underlying the increased β-lactam sensitivity of PG recycling-deficient cells. Since the PG recycling pathway of C. crescentus is already presented in detail in Figure 1, we would like to keep this figure simple and thus leave it as it is.

(11) Comments by lines:

(a) Line 192: Clarify that NagZ is also part of the rate-limiting step since there is no difference between AmiR or NagZ order of hydrolysis?

We have now omitted the statement that AmiR catalyzes the rate-limiting step in the PG recycling process, because our data do not allow definitive conclusions on this point.

(b) Line 201: Define "considerable fraction" since this is known, please and cite original reference(s).

Done.

(c) Line 203: Please also cite the primary papers where they have found that disruption of the PG recycling pathway in E. coli and P. aeruginosa doesn't result in morphological defects.

Since there are a number of papers that report PG recycling-deficient mutants of E. coli and P. aeru­ginosa, we would like to keep citing reviews to support this statement. However, we have now addi­tionally included a review by Park & Uehara (2008), which provides a detailed overview of PG recycling in bacteria.

(d) Line 220-223: Though there are no obvious morphological defects, several mutants (e.g., ΔamiR, ΔampG) appear to be lysing or stressed under minimal conditions. Could you include spotting assays and/or growth curves on minimal medium (Figure 4, Figure S2) to quantify fitness under nutrient limitation?

Have performed the requested serial dilution spot assays on minimal (M2G) medium plates and now present the data obtained in Figure 4-figure supplement 3C.

(e) Line 224: PG recycling has been found to contribute to the regulation of B-lactam resistance in several organisms, not just those two. Perhaps add "including C. freundii and P. aeruginosa"

Done.

(12) Typographical errors:

(a) Line 284: "caron" should be carbon.

Done.

(b) Line 323: "Figure C" needs a figure number.

Done.

(c) Line 33: "regulaton" should be regulation.

Done.

Reviewer #2 (Recommendations for the authors):

(1) The study is well conducted and describes a number of experiments that significantly deepen previous findings. The conclusions of this paper are mostly well supported by data, but some experiments and data analysis may need to be clarified and extended.

Thank you for this positive evaluation.

(2) The data presented in Figures 2B and 2C show activities of AmiR and NagZ using LTase-cleaved cell wall preparations. Unfortunately, the preparations tested with the two enzymes should be identical, but apparently are not. Why aren't identical preparations used?

We are sorry for the confusion. As stated in the Methods section (page 28, lines 757 and 773), the AmiR activity assays used LT products from PG sacculi isolated from E. coli D456, whereas the NagZ activity assays used LT-products from PG sacculi isolated from E. coli CS703-1. Both strains have a higher penta­peptide content than wild-type E. coli D456 lacks PBPs 4, 5 and 6 and has a moderate level of pentapeptides. CS703-1 lacks PBPs 1a, 4, 5, 6, 7 as well as AmpC and AmpH, and is known to have a higher pentapeptide content than D456. These differences are the reason for the distinct muro­peptide profiles in panel B and C of Figure 2.

(3) I am missing a control experiment where muropeptides treated with NagZ were further digested with AmiR? This would show whether AmiR is able or not to cleave MurNAc-peptides. This is not evident from the provided experiments.

We have now tested the activity of AmiR towards anhMurNAc-tetrapeptide in vitro. The results show that AmiR efficiently cleaves this GlcNAc-free anhydro-muropeptide species, verifying that it can also act on turnover products that have been previously processed by NagZ. The new data are shown in Figure 2–figure supplement 5.

(4) The claim that PG recycling is critical, particularly upon transition to the stationary phase and under nutrient limitation, is not justified. It conflicts with the obvious morphological effects also in the exponential phase and with the absence of morphological defects in minimal medium: pronounced defects in rich PYE medium (Figure 4A/B) disappear in minimal M2G medium (Figure 4_figure supplement 2). It seems that catabolite repression effects apply here. Is the morphological effect in rich PYE medium reversed by adding glucose?

We agree that PG recycling is not considerably more important in stationary phase and have removed this statement. Interestingly, while PG recycling-deficient mutants show no obvious mor­phol­ogical defects in minimal (M2G) medium, their ampicillin sensitivity even increases under this condi­tion (new Figure 4-figure supplement 3C), confirming that morphological and resistance defects are not strictly coupled. Preliminary data indicate that the morphological defects of the mutant cells are also abolished upon growth in PYE+glucose medium. High glucose availability may promote increased de novo synthesis of PG precursors, thereby partially restoring the PG precursor pool. We propose that the morphological and resistance phenotypes develop at different degrees of PG precursor depletion. However, future research is required to clarify the precise molecular basis of this phenomenon.

(5) Figure 4: Why is the contribution of AmpG to ampicillin resistance much lower than for amiR or nagZ, despite ampG mutants showing the largest morphological defects? Does the accumulation of UDP-MurNAc or UDP-MurNAc-peptide correlate with ampicillin resistance, whereas the morphological effects correlate with the lack of precursors?

The exact reason why the ΔampG mutant shows such a strong discrepancy in the severity of its morphol­ogical and resistance defects compared to the ΔamiR and ΔnagZ mutants remains unclear, because all of these deletions completely block the recycling of anhydro-muropeptides. The major difference in the ΔampG mutant is its inability to import anhydro-muropeptides, causing their accu­mu­lation in the periplasm. We propose that periplasmic anhydro-muropeptides, in particular the penta­peptide-containing species, can interact with the substrate-binding sites of PG metabolic enzymes, thereby interfering with proper PG biosyn­thesis. Conversely, by interacting with transpep­tidases, they may reduce their accessibility to ampicillin and thus preserve their acti­vity under β-lactam stress, particularly under conditions in which low PG precursor availability reduces binding site occupancy and thus facilitates antibiotic association.

Author response:

The following is the authors’ response to the previous reviews

eLife Assessment

This important study introduces an advance in multi-animal tracking by reframing identity assignment as a self-supervised contrastive representation learning problem. It eliminates the need for segments of video where all animals are simultaneously visible and individually identifiable, and significantly improves tracking speed, accuracy, and robustness with respect to occlusion. This innovation has implications beyond animal tracking, potentially connecting with advances in behavioral analysis and computer vision. The strength of support for these advances is compelling overall, although there were some remaining minor methodological concerns.

To tackle “minor methodological concerns” mentioned in the Editorial assessment and Reviewer 3, the new version of the manuscript includes the following changes:

a) The new ms does not anymore use the word “accuracy” but “IDF1 scores”. See, for example, Lines 46, 161, 176, and 522 for our new wording as “IDF1 scores”.

b) Instead of comparing softwares using mean accuracy over the benchmark, Reviewer 3 proposes to use medians or even boxplots. We now provide boxplot results with mean, median, percentiles and outliers (Figure 1- figure Supplement 2).

Additionally, we also include in the text the other recommendations from Reviewer 3:

a) We now more explicitly describe the problems of the original idtracker.ai v4 in the benchmark (lines 66-68). Around half of the videos had a high accuracy in the original dtracker.ai (v4) but the other half of the videos had lower accuracies (Figure 1a, blue). The new idtracker.ai has high accuracy values for all the videos (Figure 1a, magenta).

Also, the videos with high accuracy in the old idtracker.ai had very long tracking times (Figure 1b, blue) and the new version does not (Figure 1b, magenta). So the benchmark allows us to distinguish the new idtracker.ai as having a better accuracy for all videos and lower tracking times, making it a much more practical system than previous ones. 

b) We further clarified the occlusion experiment (lines 188-190 and 277-290).

c) We explain why we measure accuracies with and without animal crossings (lines 49-62).

d) We added a Discussion section (lines 223-244).

We believe the new version has clarified the minor methodological concerns.

Reviewer #3 (Public review):

The authors have reorganized and rewritten a substantial portion of their manuscript, which has improved the overall clarity and structure to some extent. In particular, omitting the different protocols enhanced readability. However, all technical details are now in appendix which is now referred to more frequently in the manuscript, which was already the case in the initial submission. These frequent references to the appendix - and even to appendices from previous versions - make it difficult to read and fully understand the method and the evaluations in detail. A more self-contained description of the method within the main text would be highly appreciated.

In the new ms, we have reduced the references to the appendix by having a more detailed explanation in one place, lines 49-62.

Furthermore, the authors state that they changed their evaluation metric from accuracy to IDF1. However, throughout the manuscript they continue to refer to "accuracy" when evaluating and comparing results. It is unclear which accuracy metric was used or whether the authors are confusing the two metrics. This point needs clarification, as IDF1 is not an "accuracy" measure but rather an F1-score over identity assignments.

We thank the reviewer for noticing this. Following this recommendation, we changed how we refer to the accuracy measure with “IDF1 score” in the entire ms. See, for example, lines 46, 161, 176, and 522.

The authors compare the speedups of the new version with those of the previous ones by taking the average. However, it appears that there are striking outliers in the tracking performance data (see Supplementary Table 1-4). Therefore, using the average may not be the most appropriate way to compare. The authors should consider using the median or providing more detailed statistics (e.g., boxplots) to better illustrate the distributions.

We thank the reviewer for asking for more detailed statistics. We added the requested box plot in Figure 1- figure Supplement 2 to provide more complete statistics in the comparison.

The authors did not provide any conclusion or discussion section. Including a concise conclusion that summarizes the main findings and their implications would help to convey the message of the manuscript.

We added a Discussion section in lines 223-244.

The authors report an improvement in the mean accuracy across all benchmarks from 99.49% to 99.82% (with crossings). While this represents a slight improvement, the datasets used for benchmarking seem relatively simple and already largely "solved". Therefore, the impact of this work on the field may be limited. It would be more informative to evaluate the method on more challenging datasets that include frequent occlusions, crossings, or animals with similar appearances.

Around half of the videos also had a very high accuracy in the original dtracker.ai (v4) but the other half of the videos had lower accuracies (Figure 1a, blue). For example, we found IDF1 scores of 94.47% for a video of 100 zebrafish with thousands of crossings (z_100_1), 93.77% for a video of 4 mice (m_4_2) and 69.66% for a video of 100 flies (d_100_3). The new idtracker.ai has high accuracy values for all the videos (Figure 1a, magenta).

Importantly, the tracking times for the majority of videos was very high in the original idtracker.ai (Figure 1b, blue), making the use of the tracking system limited in practice. The new system manages both a high accuracy in all videos (Figure 1a, magenta) and much lower tracking times (Figure 1b, magenta), making it a much more practical system..

We have added a sentence of the limitations of the original idtracker.ai as obtained from the benchmark, lines 66-68.

The accuracy reported in the main text is "without crossings" - this seems like incomplete evaluation, especially that tracking objects that do not cross seems a straightforward task. Information is missing why crossings are a problem and are dealt with separately.

We have now added an explanation on why we measure accuracy without crossings and why we separated it from the accuracy for all the trajectory in lines 49-62. The reason is that the identification algorithm being presented in this ms only identifies animal images outside the crossings. This algorithm makes robust animal identifications through the video despite the thousands of animal crossings typically existing in each of our videos used in the benchmark. It is a second algorithm (that hasn’t changed since the first idTracker in 2014) the one that assigns animal positions during crossings once the first algorithm has made animal identifications before and after the crossings.

There are several videos with a much lower tracking accuracy, explaining what the challenges of these videos are and why the method fails in such cases would help to understand the method's usability and weak points.

Some videos had low accuracy on previous versions (Figure 1a, blue), but the new idtracker.ai has high accuracy in all of them (Figure 1a, magenta).

Reviewer #3 (Recommendations for the authors):

(1) As described before, the authors claim to use IDF1 as their metric in the whole manuscript (lines 414-436) but only refer to accuracy when presenting the results. It is not clear, whether accuracy was used as a metric instead of IDF1 or the authors are confusing these metrics.

Following this recommendation, we replaced “accuracy” with “IDF1 score” , see lines 46, 161, 176, and 522.

(2) In the introduction, a brief explanation why crossings need to be dealt with separately would help to understand the logic of the method design.

We added such an explanation in lines 49-62.

(3) Figure 3: We asked about how the tracking accuracy is being assessed with occlusions. The authors responded with that only the GT points inside the ROI are taken into account when computing the accuracy. Does this mean, that the occluded blobs are still part of the CNN training and the clustering? This questions the purpose of this experiment, since the accuracy performance would therefore only change, if the errors, that their approach is doing either way, are outside the ROI and, therefore, not part of the metric evaluation.

The occluded blobs are not part of any training because they are erased from the video, they do not exist. We made this more clear in lines 188-190 and 277-290.

(4) Figure 1: The fact that datasets are connected with a line is misleading - there is no connection between the data along the x-axis. A line plot is not an appropriate way to present these results.

The new ms clarifies that the lines are for ease of visualization, see last line in the caption of Figure 1.

(5) Lines 38-39: It is not clear how the CNN can be pretrained for the entire video if there are no global segments or only short ones. Here, the distinction between "no segments", "only short segments" and "pretraining on the entire video" is not explained.

This pretraining protocol is not used in the version of the software we present, so details of this are not as relevant.

(6) Figure 2a: The authors are showing "individual fragments" and individual fragments in a global fragment." However, it seems there are a few blue borders missing. In the text (l. 73-79), they note, that they are displaying them as "examples" but the absence of correct blue borders is confusing.

In the new ms, we have replaced the label “Individual fragments in a global fragment” with “Individual fragments in an example global fragment” in the legend of Figure 2.

(7) Lines 61-63, 148-151, and 162-164: Could the authors clarify why they used the average instead of median when comparing the speedups of the new version and the old ones?

We thank the reviewer for asking for more detailed statistics. We added the requested box plot in Figure 1- figure Supplement 2 to provide more complete statistics in the comparison of accuracies and tracking times for old and new systems.

(8) Lines 140-144: The post-processing steps are not clear. The authors should rather state clearly which processes of the old versions they are using. Then the authors could shortly explain them.

We removed this paragraph and explained in more detail in lines 49-62 which parts of the software are new and which ones are not.

(9) Lines 239-251: Here, the authors are clarifying on a section 1-2 pages before. This information should be directly in that section instead.

Following this recommendation, we clarified the occlusion experiment in the main text (lines 188-191) to make it more self-contained. Still, the flow of the main text is better with some details in Methods.

(10) Line 38: It is not clear how the CNN can be pretrained for the entire video if there are no global segments or only short ones. Here, the distinction between "no segments"

"only short segments" and "pretraining on the entire video" is a bit misleading/underexplained.

See number 5.

(11) Figure 2a: The authors are showing "individual fragments" and individual fragments in a global fragment." However, it seems there are a few blue borders missing. In the text (l. 73-79), they note, that they are displaying them as "examples" but the absence of correct blue borders is confusing.

See number 6.

(12) Figure 2c and line 115-118: "Batches" itself is not meaningful without any information of the batch size. The authors should rather depict the batch size and then the number of epochs. The Figure 2 contains the info 400 positive and 400 negative pairs of images per batch. However, there is no information about the total number of images.

Furthermore, these metrics are inappropriate here, since training is carried out from scratch (or already pre-trained) for every new video, each video has different number of animals, different number of images.

Following this recommendation, we clarified the number of images in each batch (Figure 1c caption and lines 134-138), why we do not work with epochs (lines 700-702), and the idea that the clusters in Figure 2 represent an example and the number of batches needed for the clusters to form depends on the video details.

Appendix 1-figure 1: why do the methods fail? It looks that for certain videos the method is fairly unreliable. What is the reason for the methods to crash and how to avoid this?

Those failures are only for the old idtracker.ai and Trex, not for the method presented here. Our new contrastive algorithm does not fail in any of the videos in the benchmark.

We thank the reviewer for the detailed suggestions. We believe we have incorporated all of them in the new version of the ms.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This paper by Karimian et al proposes an oscillator model tuned to implement binding by synchrony (BBS*) principles in a visual task. The authors set out to show how well these BBS principles explain human behavior in figure-ground segregation tasks. The model is inspired by electrophysiological findings in non-human primates, suggesting that gamma oscillations in early visual cortex implement feature-binding through a synchronization of feature-selective neurons. The psychophysics experiment involves the identification of a figure consisting of gabor annuli, presented on a background of gabor annuli. The participants' task is to identify the orientation of the figure. The task difficulty is varied based on the contrast and density of the gabor annuli that make up the figure. The same figures (without the background) are used as inputs to the oscillator model. The authors report that both the discrimination accuracy in the psychophysics experiment and the synchrony of the oscillators in the proposed model follow a similar "Arnold Tongue" relationship when depicted as a function of the texture-defining features of the figure. This finding is interpreted as evidence for BBS/gamma synchrony being the underlying mechanism of the figure-ground segregation.

Note that I chose to use "BBS" over gamma synchrony (used by the authors) in this review, as I am not convinced that the authors show evidence for synchronization in the gamma-band.

We thank the reviewer for their careful assessment of our manuscript and useful comments that we believe have served to strengthen our work.

Strengths:

The design of the proposed model is well-informed by electrophysiological findings, and the idea of using computational modeling to bridge between intracranial recordings in non-human primates and behavioral results in human participants is interesting. Previous work has criticized the BBS synchrony theory based on the observation that synchronization in the gamma-band is highly localized and the frequency of the oscillation depends on the visual features of the stimulus. I appreciate how the authors demonstrate that frequency-dependence and local synchronization can be features of BBS, and not contradictory to the theory. As such, I feel that this work has the potential to contribute meaningfully to the debate on whether BBS is a biophysically realistic model of feature-binding in visual cortex.

Weaknesses:

I have several concerns regarding the presented claims, assessment of meaning and size of the presented effects, particularly with regard to the absence of a priori defined effect sizes.

Firstly, the paper makes strong claims about the frequency-specificity (i.e., gamma synchrony) and anatomical correlates (early visual cortex) of the observed effects. These claims are informed by previous electrophysiological work in non-human primates but are not directly supported by the paper itself. For instance, the title contains the word "gamma synchrony", but the authors do not demonstrate any EEG/MEG or intracranial data in from their human subjects supporting such claims, nor do they demonstrate that the frequencies in the oscillator model are within the gamma band. I think that the paper should more clearly distinguish between statements that are directly supported by the paper (such as: "an oscillator model based on BBS principles accounts for variance in human behavior") and abstract inferences based on the literature (such as "these effects could be attributed to gamma oscillations in early visual cortex, as the model was designed based on those principles").

We thank the reviewer for this helpful comment and agree that the scope of our claims should be clearly delineated between what is directly supported by our data and what is theoretically inferred from prior literature.

We revised the Abstract, Introduction, and early Discussion to moderate the strength of our statements and make the distinction explicit. The revised title now emphasizes that our study tests principles derived from prior work on gamma synchrony rather than directly demonstrating gamma activity in humans. Throughout the text, we use more cautious phrasing that highlights potential mechanisms and theoretical predictions. The intention of our study was not to position synchrony as the only viable mechanism of figure–ground perception. Rather, our goal was to reinvigorate it as a potential contender by showing that features often cited as limitations of synchrony-based binding may in fact be essential properties of the mechanism. We updated phrasing throughout the manuscript to make this clearer and avoid overstating the study’s contribution.

Importantly, our model is not agnostic with respect to frequency band. Oscillator frequencies exhibited by model units are within the gamma range by design. Frequency emerges directly from the contrast within each oscillator’s receptive field, following an empirically established relationship between stimulus contrast and gamma frequency. To our knowledge, such a robust, quantitative relationship between stimulus features to exact oscillation frequency has not been consistently demonstrated for other frequency bands. This relationship yields gamma-band frequencies for all contrasts used in our simulations. The model is thus indeed a gamma oscillator model of V1, not a generic instantiation of Binding by Synchrony (BBS) principles.

That said, we fully agree with the reviewer that our study cannot demonstrate a direct link between gamma synchrony in visual cortex and human behavior. Our behavioral and modeling results instead show that synchronization principles derived from gamma-band physiology in V1 can predict perceptual performance patterns. We now make this distinction explicit throughout the revised manuscript.

Secondly, unlike the human participants, the model strictly does not perform figure-ground segregation, as it only receives the figure as an input.

We thank the reviewer for the opportunity to clarify our modeling approach. We chose not to model the background to reduce computational cost, since including it requires a substantially larger number of oscillators without changing the model’s predictions. The model thus indeed only receives the figure region as input. We aimed to test the local grouping mechanism predicted by TWCO, rather than to simulate a full figure–ground segregation process including a read-out stage. Our model therefore isolates the conditions under which local synchrony emerges within the figure region, assuming that a downstream read-out mechanism (not explicitly modeled here) would detect regions of coherent activity. The exact nature of such a read-out mechanism was beyond the scope of our work.

To confirm that our simplified model is a valid proxy, we ran additional simulations including the background and found that a coherent figure assembly reliably emerges, as can be seen in the phase-locking patterns relative to a reference oscillator at the center of the figure. This validates that the principles of local grouping we studied in isolation hold even when the figure is embedded in a noisy surround. We have added an explicit note in the Results (paragraph 2) that we only simulate the figure and added Supplementary Figure S1 showing the additional simulations.

Finally, it is unclear what effect sizes the authors would have expected a priori, making it difficult to assess whether their oscillator model represents the data well or poorly. I consider this a major concern, as the relationship between the synchrony of the oscillatory model and the performance of the human participants is confounded by the visual features of the figure. Specifically, the authors use the BBS literature to motivate the hypothesis that perception of the texture-defined figure is related to the density and contrast heterogeneity of the texture elements (gabor annuli) of the figure. This hypothesis has to be true regardless of synchrony, as the figure will be easier to spot if it consists of a higher number of high-contrast gabors than the background. As the frequency and phase of the oscillators and coupling strength between oscillators in the grid change as a function of these visual features, I wonder how much of the correlation between model synchrony and human performance is mediated by the features of the figure. To interpret to what extent the similarity between model and human behavior relies on the oscillatory nature of the model, the authors should find a way to estimate an empirical threshold that accounts for these confounding effects. Alternatively, it would be interesting to understand whether a model based on competing theories (e.g., Binding by Enhanced Firing, Roelfsema, 2023) would perform better or worse at explaining the data.

We thank the reviewer for these insightful and constructive comments, which have prompted additional analyses that we believe substantially strengthen our work. The reviewer raises two main points: (1) the need for a benchmark to assess our model’s performance, and (2) the concern that the relationship between model synchrony and behavior might be a non-causal “confound” of the visual features. We address each point below.

(1) Benchmarking model performance

We agree that it is important to assess how well our model performs relative to the data and included this in the original manuscript. We did not predefine an absolute good fit threshold because absolute agreement depends on irreducible noise and inter-subject variability, making a universal cutoff arbitrary. Instead, we had benchmarked model performance in two complementary ways. First, the noise ceiling shown in Figure 5 provides an empirical benchmark for the maximum fit any model could achieve on our data. Simulated Arnold tongues (based on synchrony) approach this ceiling achieving 89% of possible similarity for correlation and 79% of possible similarity for weighted Jaccard similarity, respectively. Second, the parameter sweep (Figure 3) situates our model’s performance within the broader parameter space. It shows that the model, whose key parameters were fixed a priori from independent macaque neurophysiological data, lies close to the optimal regime for explaining the human data. It also provides an estimate of the lower bound (worst-performing point) on the fit that a misspecified model implementing the identical mechanism would achieve. Our model with fixed a priori parameters does 1.41 times better than a misspecified model for the correlation fit metric and 3 times better for weighted Jaccard similarity.

(2) Synchrony as mechanism vs. potential confound

We appreciate the reviewer’s suggestion to test whether synchrony explains behavior beyond stimulus features. In our framework, synchrony is a near-deterministic function of the manipulated stimulus features given fixed model parameters. As a result, synchrony and the stimulus features are collinear (R²≈0.8) leaving no independent variance for synchrony to explain once stimulus features are included. Adding both into one statistical model yields unstable coefficients and no out-of-sample improvement.

Mechanistically, we believe the relevant question is not whether synchrony explains behavior beyond stimulus features but whether synchrony is the correct transformation of the stimulus features to reproduce the behavioral pattern. Please note that in our design we ensured that mean contrast and luminance are identical in the figure and the background such that there are not more high-contrast Gabors in the figure than in the background. We did this with the aim to render mean contrast not a relevant feature. However, there are more high-contrast Gabors in the background, and it is conceivable that the absence of such high contrasts in the figure drives the detection/discrimination of the figure. We therefore agree that testing alternative models would further clarify the unique explanatory value of the synchrony mechanism. To that end, we derived two alternative rate-based readouts from the same V1 simulations of our model from which we derived synchrony. First, average firing rates inside the figure and second, the difference between average firing rates inside the figure and average firing rates in the background (rate difference). We analyzed each individually as predictors of behavior and performed a model comparison based on out-of-sample predictions. While rate difference (but not average firing) showed meaningful associations with performance when considered alone, the synchrony readout had a larger effect size and was favored by the model comparison. We added a new subsection comparing synchrony to rate-based alternatives in the Results (paragraphs 7-9), including additional Bayesian analyses and LOO-CV model comparison. Please note that the model comparison we added to the manuscript provides an additional benchmark beyond the map-level ceiling analysis. It indicates that the mapping from stimulus features to behavior via synchrony generalizes best without requiring an a priori good-fit threshold.

We agree that formally comparing our model to a sophisticated rate-based alternative, such as an instantiation of the Binding by Enhanced Firing model, is an important direction for future work. However, it remains an open and non-trivial question whether such a model could quantitatively reproduce the precise shape of the behavioral Arnold tongue that emerges from the systematic manipulation of our stimulus parameters. Implementing and parameterizing such a model in a comparable, biologically grounded framework is a substantial undertaking that lies beyond the scope of the current study. Therefore, our goal here was not to claim exclusivity for synchrony-based mechanisms, but rather to re-evaluate their plausibility by showing that features often seen as limitations (stimulus dependence and frequency heterogeneity) are, in fact, essential characteristics of the TWCO framework that can predict complex behavioral outcomes.

We would also like to clarify that our stimulus features were derived from theory rather than psychophysical literature. Starting from the principles of TWCO, we mapped frequency detuning and coupling strength onto known anatomical and physiological properties of early visual cortex, and only then derived the corresponding stimulus manipulations (contrast heterogeneity and grid coarseness). Demonstrating that these features predict behavior is therefore not trivial but constitutes a first empirical confirmation that the core TWCO variables match perception.

Apart from adding analyses of additional rate-based readouts of our model, we also refined our discussion of the relationship between these and a synchrony-based mechanism.

Reviewer #2 (Public review):

The authors aimed to investigate whether gamma synchrony serves a functional role in figure-ground perception. They specifically sought to test whether the stimulus-dependence of gamma synchrony, often considered a limitation, actually facilitates perceptual grouping. Using the theory of weakly coupled oscillators (TWCO), they developed a framework wherein synchronization depends on both frequency detuning (related to contrast heterogeneity) and coupling strength (related to proximity between visual elements). Through psychophysical experiments with texture discrimination tasks and computational modeling, they tested whether human performance follows patterns predicted by TWCO and whether perceptual learning enhances synchrony-based grouping.

We thank the reviewer for their thoughtful and constructive review. We believe the comments have served to improve our work.

Strengths:

(1) The theoretical framework connecting TWCO to visual perception is innovative and well-articulated, providing a potential mechanistic explanation for how gamma synchrony might contribute to both feature binding and separation.

(2) The methodology combines psychophysical measurements with computational modeling, with a solid quantitative agreement between model predictions and human performance.

(3) In particular, the demonstration that coupling strengths can be modified through experience is remarkable and suggests gamma synchrony could be an adaptable mechanism that improves with visual learning.

(4) The cross-validation approach, wherein model parameters derived from macaque neurophysiology successfully predict human performance, strengthens the biological plausibility of the framework.

Weaknesses:

(1) The highly controlled stimuli are far removed from natural scenes, raising questions about generalisability. But, of course, control (almost) excludes ecological validity. The study does not address the challenges of natural vision or leverage the rich statistical structure afforded by natural scenes.

We agree with the reviewer that the insights of the present study are limited to texture stimuli and have made adjustments in the Discussion (final two paragraphs) to avoid claiming generalizability to natural stimuli. We have also adjusted the title to specifically limit our results to texture stimuli. To establish the principles of TWCO, we needed tight control over the stimulus, but are intrigued by the idea to investigate natural scenes. We have added to our Discussion (paragraph 9) that future should evaluate to what extent the principles we investigate here apply to natural scenes. Synchrony-based mechanisms have been successfully used for image segmentation tasks in machine vision, showing that the proposed mechanism can in principle work for natural scenes.

(2) The experimental design appears primarily confirmatory rather than attempting to challenge the TWCO framework or test boundary conditions where it might fail.

We thank the reviewer for this important point. Our primary motivation was to address the neurophysiological properties of gamma synchrony that have been suggested to severely challenge the binding by synchrony mechanism. Particularly the strong dependence of gamma oscillations and synchrony on stimulus features. Our goal was to show that from the perspective of TWCO, these challenges become expected components of the mechanism. In essence, we wanted to promote a conceptual shift that converts what pushes a theory to its limit into something that is actually its central tenet. To facilitate this shift, we designed the experiment to directly test this core tenet.

While our approach was designed to test a central prediction of TWCO rather than explicitly challenge its boundaries, we respectfully argue that it was far from a simple confirmatory experiment. The design incorporated high-risk elements that provided considerable room for both the theory and our model to fail. First, the core prediction itself was non-obvious and highly specific. We did not simply test whether contrast heterogeneity and grid coarseness affect perception. We tested the stronger hypothesis that they would reflect a specific, interactive trade-off (the behavioral Arnold tongue) as specified by TWCO. Second, our modeling approach was deliberately constrained to provide a further stringent test. We did not post-hoc optimize the model's key parameters to fit our behavioral data. Instead, we fixed them a priori based on independent neurophysiological data from macaques. This was a high-risk choice, as a mismatch between a priori model predictions and the human data would have seriously challenged the framework's generalizability.

We agree that future research should further challenge TWCO. For instance, by using stimuli that require segregating several objects simultaneously or objects that cover more extensive regions of the visual field.

(3) Alternative explanations for the observed behavioral effects are not thoroughly explored. While the model provides a good fit to the data, this does not conclusively prove that gamma synchrony is the actual mechanism underlying the observed effects.

We agree that our results do not conclusively show that gamma synchrony is the actual mechanism underlying figure-ground segregation. We admit that the original phrasing used throughout the manuscript was too strong and gave the impression that we wanted to establish exactly that. However, the goal of our work was only to reinvigorate gamma synchrony as a potential contender by showing that features often cited as limitations of synchrony-based binding may in fact be essential properties of the mechanism. We have revised the title and made adjustments throughout the manuscript to better reflect this more moderate goal.

Additionally, we added tests of alternatives (Results, paragraphs 7–9) to clarify the unique explanatory value of the synchrony mechanism. To that end, we derived two alternative rate-based readouts from the same V1 simulations of our model. First, we extracted average firing rates inside the figure. Second, we computed the difference between average firing rates inside the figure and average firing rates in the background (rate difference). We analyzed each individually as predictors of behavior and performed a model comparison between these two and synchrony based on out-of-sample predictions. While the rate difference (but not average firing) showed meaningful associations with performance when considered alone, the synchrony readout had a larger effect size and was favored by the model comparison.

(4) Direct neurophysiological evidence linking the observed behavioral effects to gamma synchrony in humans is absent, creating a gap between the model and the neural mechanism.

We agree that the model only provides a how-possibly account linking stimulus features to performance. Showing that the brain actually relies on this mechanism would require showing that cortical synchrony mediates the effect of stimulus features on behavior beyond firing rates. Collecting such data would constitute a major effort that would go beyond the scope of this study. We acknowledge the need for electrophysiological data and the mediation analysis in the updated Discussion.

Achievement of Aims and Support for Conclusions:

The authors largely achieved their primary aim of demonstrating that human figure-ground perception follows patterns predicted by TWCO principles. Their psychophysical results reveal a behavioral "Arnold tongue" that matches the synchronization patterns predicted by their model, and their learning experiment shows that perceptual improvements correlate with predicted increases in synchrony.

The evidence supports their conclusion that gamma synchrony could serve as a viable neural grouping mechanism for figure-ground segregation. However, the conclusion that "stimulus-dependence of gamma synchrony is adaptable to the statistics of visual experiences" is only partially supported, as the study uses highly controlled artificial stimuli rather than naturalistic visual statistics, or shows a sensitivity to the structure of experience.

Likely Impact and Utility:

This work offers a fresh perspective on the functional role of gamma oscillations in visual perception. The integration of TWCO with perceptual learning provides a novel theoretical framework that could influence future research on neural synchrony.

The computational model, with parameters derived from neurophysiological data, offers a useful tool for predicting perceptual performance based on synchronization principles. This approach might be extended to study other perceptual phenomena and could inspire designs for artificial vision systems.

The learning component of the study may have a particular impact, as it suggests a mechanism by which perceptual expertise develops through modified coupling between neural assemblies. This could influence thinking about perceptual learning more broadly, but also raises questions about the underlying mechanism that the paper does not address.

Additional Context:

Historically, the functional significance of gamma oscillations has been debated, with early theories of temporal binding giving way to skepticism based on gamma's stimulus-dependence. This study reframes this debate by suggesting that stimulus-dependence is exactly what makes gamma useful for perceptual grouping.

The successful combination of computational neuroscience and psychophysics is a significant strength of this study.

The field would benefit from future work extending (if possible) these findings to more naturalistic stimuli and directly measuring neural activity during perceptual tasks. Additionally, studies comparing predictions from synchrony-based models against alternative mechanisms would help establish the specificity of the proposed framework.

Recommendations for the authors:

Reviewing Editor Comments:

In a joint discussion to integrate the peer reviews and agree on the eLife recommendations, both reviewers agreed that the work is valuable, but they were on the fence about whether the strength of evidence was incomplete or solid, eventually settling on incomplete. The reviewers make several recommendations for improving these ratings, which I (Reviewing Editor) have organised into 3 points below, with point 1 of particular importance. Underneath the summary, please see the individual recommendations of the reviewers.

(1) Strengthen evidence for the unique role of gamma synchrony in explaining the data, and ensuring claims are directly supported by relevant data:

Reviewers 2 and 3 both note the lack of direct evidence for gamma involvement, and reviewer 2 observes that the fit with behaviour may trivially be explained by a relationship between contrast heterogeneity and grid coarseness without need for oscillation. The reviewers felt that the approach of fitting the model to human data could be strengthened to help address this issue - and they offer various solutions, e.g., more principled a-priori criteria around good vs bad fit of the model to both main task and training data, and comparison to alternative binding models (Reviewer 2), identifying and testing boundary conditions of the model (Reviewer 3). There is also the possibility of collecting direct human neurophysiological evidence linking the behavioural data to neural mechanisms. Our discussion also highlighted the need to weaken claims (including in the title) where links are not directly demonstrated by methods from the present study, e.g., resting on indirect comparisons to primate literature.

We agree with the editor and reviewers that this was a critical point. To address it, we have made several major revisions.

As suggested, we have weakened claims where the links are not directly demonstrated by our data. The title has been revised to be more specific, and we have carefully edited the abstract, introduction, and discussion to distinguish between our model's predictions and direct neurophysiological evidence.

To address the concern that our model's fit might be trivially explained by visual features, we have performed a new analysis comparing the synchrony-based readout to two alternative rate-based readouts from the same V1 simulations. This new comparison shows that the synchrony readout provides a superior out-of-sample prediction of human behavior.

While a full implementation of a competing theory like "Binding by Enhanced Firing" would be a valuable next step, we note that parameterizing such a model in a comparably grounded framework is a substantial undertaking beyond the scope of the present study. Our new analysis provides an important first step in this direction.

(2) Make explicit and address the limitations of the stimuli:

Include that the model is not extracting the figure from the background, and the controlled stimuli may limit generalizability.

To address the concern that our model was not performing true figure-ground extraction, we performed a new set of simulations that included both the figure and the immediate background. The results confirm that synchrony dynamics within the figure region are not affected by the presence of the background. We added these validation results as supplementary materials. We have additionally made the modeling choice and its justification more explicit in the Results and Methods sections.

We have revised the Discussion to be more explicit about the limitations of using highly controlled texture stimuli. We now clearly state that our findings are specific to this context and that further research is required to determine if these principles generalize to the segregation of objects in natural scenes.

(3) Some clarifications to make more accessible:

Include the figure explaining the framework (Reviewers 1&2), and also the model details (Reviewer 2).

We have revised Figure 1 and its caption to more clearly illustrate the links from TWCO principles to their neural implementation in V1 and the resulting behavioral predictions.

We have expanded the Methods section to provide a more detailed and accessible description of the model's construction. We now clarify precisely how the oscillator grid was defined in visual space, how eccentricity-dependent receptive field sizes were implemented, and how these were mapped onto a retinotopic cortical surface to determine coupling strengths.

Reviewer #1 (Recommendations for the authors):

(A) Major concerns:

(1) My main concern:

My main concern is the repeated claims that the observed findings can be attributed to gamma synchrony in the early visual cortex. I find this claim misleading as the authors do not report any electrophysiological data that directly supports such claims. As stated in my public review, I feel that the authors should be clear about direct evidence versus more abstract inferences based on the literature.

In particular, I recommend changing claims about "gamma synchrony" to "Binding by Synchrony" That being said, the authors can outline that the model was built under the assumption that this synchrony is mediated by gamma in early visual cortex, but I don't think it should be part of their main conclusions.

We appreciate that TWCO’s general principles are frequency-agnostic and can be viewed as binding by synchrony in a broad sense. Our work, however, specifically instantiates these principles in V1 gamma: the model reflects TWCO dynamics together with V1 anatomy/physiology and the well-established contrast–frequency relationship in the gamma range (which, to our knowledge, has not been demonstrated with comparable specificity for other bands). In that sense, it is a gamma oscillator model of V1, rather than a generic BBS instantiation. Moreover, stimulus dependencies often cited as challenges to BBS have been used in particular to argue against gamma; showing that these very dependencies are integral to the TWCO mechanism is central to our contribution, and we therefore keep our conclusions focused on the gamma-specific instantiation tested here.

(2) Mediation of the observed effects by the visual features of the figure:

The authors motivate the hypothesis that BBS predicts that the perception of texture-defined objects depends on the density of texture elements and their contrast heterogeneity. This hypothesis seems trivial as those are the features that distinguish figure from ground. I think it would be important to clarify how this hypothesis is unique to BBS and not explained by competing theories, such as Binding by Enhanced Firing (Roelfsema, 2023). The authors should be clear about what part of the hypothesis is not trivial based on the task and clearly attributable to oscillators and synchrony.

Our stimulus features were derived from theory rather than psychophysical literature. Starting from the principles of TWCO, we mapped frequency detuning and coupling strength onto known anatomical and physiological properties of early visual cortex, and only then derived the corresponding stimulus manipulations (contrast heterogeneity and grid coarseness). We agree that grid coarseness (element distance) is an established facilitator of figure–ground perception. By contrast, contrast heterogeneity (feature variance) is less commonly emphasized as a figure–ground cue, compared to mean-based cues, but follows directly from TWCO’s frequency detuning. Importantly, mean contrast and luminance were matched exactly between figure and background in our stimuli. Demonstrating that contrast heterogeneity and grid coarseness not only independently affect figure-ground perception, but reflect a trade-off where higher heterogeneity needs to counteracted by reduced grid coarseness in the way TWCO specifies is therefore non-obvious and provides an initial empirical indication that the core TWCO variables might shape perception. We also agree that alternative models would further clarify the unique explanatory value of synchrony. In the revised manuscript, we compare rate-based readouts (mean figure rate; figure–background rate difference) with the synchrony readout from the same simulations. Rate difference indeed constitutes a predictor of performance, but the synchrony readout showed a larger effect and was preferred by out-of-sample model comparison.

Using a linear model, the authors assess the relationship between discrimination accuracy and synchrony. Did the authors also include the factors grid coarseness and contrast heterogeneity in this model? Again, as both the task performance (as shown by the GEE analysis) and oscillatory synchrony depend on these features, the relationship between model and behavioral performance will be mediated by the visual features.

Thank you for raising this. In our framework, detuning (via contrast heterogeneity) and coupling (via grid coarseness) are the inputs, synchrony is the proposed mechanistic mediator, and behavior is the output. Because synchrony in our model is a (near-)deterministic function of the manipulated features under fixed parameters, a joint features+synchrony regression is statistically ill-posed (perfect multicollinearity up to numerical error) and cannot add information. A proper mediation test would require trial-wise neural measurements of synchrony in the same task, which we do not have and acknowledge as a limitation in the Discussion. Accordingly, we show that both the features themselves (reflecting TWCO principles) and model-derived synchrony (realizing the proposed pathway) account for behavior.

We agree this does not establish a unique contribution of synchrony. To probe alternatives, we added rate-based readouts and a model comparison to the revised manuscript. These additional analyses indicate that synchrony outperforms simple rate-based mappings. We do not claim this rules out more sophisticated rate-based mechanisms. Our aim is to demonstrate that synchrony is a viable, behaviorally informative readout for downstream processing. We do not assert it is the only mechanism the brain uses. Synchrony had been discounted due to its stimulus dependence; our results are intended to rule it back in. We have made changes throughout the manuscript to better reflect this more modest aim.

(3) Goodness of fit measures are not established a prior:

I have described this concern in my public review. It is hard to assess what the authors would have interpreted as a good or a bad fit, especially without accounting for the confound in the relationship between oscillator synchrony and behavior. Similarly, when assessing the similarity between the behavioral and dynamic Arnold Tongues across different coupling parameters, the authors found that the chosen parameters (based on macaque data) were not optimal. They offer the explanation that the human cortex has a lower coupling decay than the macaque cortex, and the similarity is higher for lower values of coupling decay. While this explanation is not entirely implausible, it is unclear where an oscillator model with human values would be in the presented plot, as the authors didn't estimate those values from the human studies. Moreover, the task used in the Lowet et al., 2017 paper is very different from the task presented here, which could also account for differences. Overall, the explanation appears hand-wavy considering the lack of empirically defined goodness of fit measures.

Thank you for these concerns.

We did indeed not provide a priori thresholds for what would be considered good fit. Instead, we used two complementary benchmarks; namely noise ceilings and parameter exploration. The former provides an upper bound on what any model (not just ours but based on completely different mechanisms) could achieve given our data. The parameter sweep provides an indication how well our concrete model can maximally fit the data and how bad it can be based on possible parameters. These benchmarks are more informative than a fixed a-priori cutoff, which would depend on unknown noise and inter-subject variability. Both the noise ceiling and the parameter exploration indicate that our model, using a priori fixed parameters, performs well. Additionally, we redid all our statistical analyses after z-normalizing every predictor to provide easier interpretation of effect sizes.

Regarding the reason that key model parameters were not optimal, we believe our interpretation to be plausible. We agree that we currently do not have data to estimate the exact human decay factor and hence cannot establish how much model fit would be affected. However, the parameter exploration in Figure 3 shows that small to modest reductions in decay would improve model fit. We discuss this now in the revised manuscript.

The reviewer’s suggestion is intriguing. While Lowet et al. (2017) used a different task, the parameters we took from their work (decay rate and maximum coupling) are intended to reflect anatomical properties and thus should not be task-dependent. That said, Lowet et al. ‘s data carry uncertainty, so our estimates may not be exact; we note this explicitly in the revised Discussion. Whether a different task would have yielded better parameter estimates is difficult to determine, but we considered Lowet’s paradigm appropriate because it was designed to target the same V1 anatomical and physiological properties that map onto TWCO.

I have concerns about a similar confound in the training effects. If I'm not mistaken, the Hebbian Learning rule encourages synchronization between the oscillators in the grid. As such, it causes synchronization to increase over several simulations. Clearly, the task performance of the participants also improves over the sessions. Again, an empirical threshold would be required to assess whether the similarity in learning between model and performance goes beyond what is expected based on learning alone. How much of these effects can be attributed to the model being oscillatory?

The reviewer is correct that, in our framework, learning operates via changes in coupling that increase synchrony. Enhanced synchrony is the proposed (and in our model also the actual) pathway by which learning impacts behavior. We agree that learning could, in principle, act through pathways other than synchrony. Demonstrating this would not be achieved by a mediation analysis here, because that requires independent, trial-level neural measurements of the candidate pathways (synchrony and alternatives). In the absence of such data, the appropriate approach would be model comparison between competing mechanistic readouts. We have added such a model comparison for a synchrony readout versus two rate-based readouts derived from the same simulations for the first session; i.e., focusing on the pathway from stimulus features to behavior. However, a similar model comparison is not possible for learning. As we show in the supplementary materials, rate-based readouts of our V1 model are not at all affected by coupling strength. As such, they are insensitive to changes in coupling and are thus not viable as alternative mechanisms to explain performance changes due to learning. A fair test of rate-based alternatives would require building a detailed rate-based figure–ground segregation model that predicts session-wise changes. We agree that this is an important next step but it is also substantial undertaking beyond the scope of the present study.

(4) Similarly, for the comparison of the Arnold Tongue in the transfer session and the early session:

In the first part of the Results section, it says: "Our model rests on the assumption that learning-induced structural changes in early visual cortex are specific to the retinotopic locations of the trained stimuli. We evaluated whether this assumption holds for our human participants using the transfer session following the main training period. [...] If learning is indeed local, participants' performance in the transfer session should resemble that of early training sessions, indicating a reset in performance for the new retinal location."

The authors find that a model fit to session 3 explains the data in the transfer session best and consider this as evidence for the above-stated expectation. Again, it is unclear where the cutoff would have been for a session to be declared as early or late. For instance, had the participants only performed 4 sessions, would the performance be best explained by session 3 or session 1?

A high number of statistical tests are used, which, firstly, need to be corrected for multiple comparisons (did the authors do this?). Secondly, I feel that the regression models could be improved. For instance, the authors fit one model per session and then assess how well each model explains the variance in the transfer session. I think the authors might want to opt for one model with the regressors contrast heterogeneity, grid coarseness, and session (and their interaction). Using this approach, the authors would still be able to assess which session predicts the data best. Similarly, interindividual variability could be accounted for by adding participant-specific random effects to the model (and using a mixed model), instead of fitting individual models per participant.

We agree the “early vs late” cutoff was underspecified. In the revision, we predefine Session 2 as the early-learning reference, excluding Session 1 to avoid familiarization/response–mapping effects. We then fit a single Bayesian hierarchical model with contrast heterogeneity, grid coarseness, and session, plus a transfer indicator, and participant-level random effects. This allows us to place the transfer session on the same scale as training and to test a) whether the transfer session precedes the state in session 2 via the posterior contrast P(βtransfer<βSess2) and b) whether it is indistinguishable from the state in session two using an equivalence test derived from the fitted model. We find that the transfer session is equivalent to session 2. We added this updated analysis of the transfer session in the Results (paragraph 15).

In response to the suggestion to use a hierarchical regression model for analyzing the transfer session, we have decided to use such a model for all our analyses in a Bayesian framework. In this Bayesian framework, inference is based on the joint posterior (credible intervals/equivalence) of all predictors in a model and additional post-hoc multiplicity corrections are not required.

(5) Questions regarding the model:

What does it mean that the grid was "defined in visual space"? How biologically plausible with regard to the retinotopy and organization of the oscillators do the authors claim the model to be?

We are happy to clarify this point. We have a total of 400 oscillators reflecting neural assemblies in V1. We start by defining a regular, 20x20, grid of the receptive field (RF) centers of these oscillators inside the figure region. Each oscillator is then also assigned a RF size based on the eccentricity of its RF center. We use the threshold-linear relationship between RF eccentricity and RF size reported in [1] to assign RF sizes. Each oscillator thus has an individual, eccentricity-dependent, RF size.

For the coupling between oscillators, we need to know their cortical distances. We obtain these by first determining the cortical location of each oscillator through a complex-logarithmic topographic mapping of neuronal receptive field coordinates onto the cortical surface [2,3]. For this mapping, we use human parameter values estimated by [4]. From these cortical locations, we then compute pairwise Euclidean distances.

The model thus captures realistic retinotopy, eccentricity-dependent RF sizes, and distance-dependent coupling on the cortical surface. We have adjusted our Methods to make these steps clearer.

(1) Freeman, J., & Simoncelli, E. P. (2011). Metamers of the ventral stream. Nature neuroscience, 14(9), 1195-1201.

(2) Balasubramanian, M., & Schwartz, E. L. (2002). The isomap algorithm and topological stability. Science, 295(5552), 7. https://doi.org/10.1126/science.1066234

(3) Schwartz, E. L. (1980). Computational anatomy and functional architecture of striate cortex: a spatial mapping approach to perceptual coding. Vision Research, 20(8), 645–669. http://www.sciencedirect.com/science/article/pii/0042698980900905

(4) Polimeni, J. R., Hinds, O. P., Balasubramanian, M., van der Kouwe, A. J. W., Wald, L. L., Dale, A. M., & Schwartz, E. L. (2005). Two-dimensional mathematical structure of the human visuotopic map complex in V1, V2, and V3 measured via fMRI at 3 and 7 Tesla. Journal of Vision, 5(8), 898. https://doi.org/10.1167/5.8.898

Similarly, do the authors claim that each gabor annuli stimulates a single receptive field in V1?

We hope that with the additional explanation above, it is clearer that there is not a one-to-one mapping. Each oscillator samples the local image by pooling over all Gabor annuli that overlap its receptive field (partially or fully) and computes the average contrast within its RF. Conversely, a single annulus typically overlaps multiple RFs and contributes to each in proportion to the overlap.

I am unsure how the oscillators were organized, if not retinotopically. How is the retinotopic input fed into the non-retinotopically arranged oscillators?

We hope that with the additional explanation above, it is clearer that the network is strictly retinotopic.

The frequency of each oscillator changes according to ω=2πv with ν=25+0.25C. How were the values for the linear regression in v chosen? Reference?

The slope and intercept parameters for this equation were first reported in [5]. We added the reference to the Methods.

(5) Lowet, E., Roberts, M., Hadjipapas, A., Peter, A., van der Eerden, J., & De Weerd, P. (2015). Input-dependent frequency modulation of cortical gamma oscillations shapes spatial synchronization and enables phase coding. PLoS computational biology, 11(2), e1004072.

(6) Hebbian Learning Rule:

I am confused about how the effective learning rate E= ∈t is calculated. It is said that it is estimated based on the similarity between the second experimental session and the distribution of synchrony after letting the model learn. How can the model learn without knowing epsilon and t?

We agree with the reviewer that our procedure to estimate the effective learning rate requires further clarification. We performed a nested grid search. Essentially, we let the model learn between session 1 and 2 with each of 25 candidate effective learning rates and evaluate how well each of them allow the model to fit performance in session 2. We then select the best effective learning rate and create a new, smaller, grid around this value and repeat that procedure. In total we perform 5 nested grids to arrive at the final effective learning rate. We expanded the explanation in the Methods.

(B) Minor concerns:

(1) Small N: 2/3 of the studies that were cited to justify the small sample were notably different from the current experiment, i.e., Intoy 2020 is an eye movement task, Lange 2020 is a memory task (Tesileanu 2020 is more similar). I think a power analysis would be great to support, as the sample size seems quite low

Our study uses a within-subject design with ~750 trials per session (≈6,000 total) per participant, analyzed with a hierarchical model that pools information across trials and participants. To assess adequacy, we ran a simulation-based design analysis using the fitted hierarchical model (i.e., post hoc, based on the observed variance components). This analysis indicated a detection probability >90% for all key effects. We now report the results of this design analysis in the (Supplementary Table 1) and note this in the Results (paragraph 1).

Regarding the literature context, we agree the cited studies are not identical to ours; we referenced them to illustrate a common practice (small N with many trials) when targeting low-level, early-visual mechanisms. Intoy (pattern/contrast sensitivity) and Lange (perceptual learning in early vision) share that focus, while Tesileanu is methodologically closest.

(2) Figure 1 could be more informative and better described in the text. The authors often don't refer to the panels in Figure 1. Maybe it would help to swap a and b to describe the Arnold tongue first? It might also be a good idea to add the coupling strength and frequency detuning axes

We have swapped panels a and b and now refer to each panel in the main text to enhance clarity.

(3) Values of rho (distance - is this degrees visual angle)? Do the authors assume that the size of the stimuli corresponds to receptive fields in V1? If so, how is this justified?

The center-to-center distance between any pair of neighboring annuli is indeed expressed in degrees of visual angle. Rho is a scaling factor for this distance. With rho=1, the center-to-center distance corresponds to the diameter of the annuli; i.e., they touch but do not overlap each other. We do not assume any relation between the size of receptive fields and the size of the annuli. Receptive field sizes in our model are purely determined by their eccentricity and each oscillator can have several annuli within its receptive field while each annulus can fall within several overlapping receptive fields of different oscillators. We believe that the schematic illustration in Figure 1 might have given the impression that each oscillator sees exactly one annulus and added a note that this is not the case and merely an oversimplification to illustrate the relationship between contrast and intrinsic frequency.

(4) Some equations are embedded in the text, and some are not. It might be easier to find the respective equation if they all have an index. For instance, the authors mention the psychometric function that relates model synchrony and performance in the results section. It would be easier to find if it had an index that the authors could refer to.

We moved this equation as well as the contrast intrinsic frequency mapping from inline to displayed and numbered them.

(5) Is there a reference for "Our model rests on the assumption that learning-induced structural changes in early visual cortex are specific to the retinotopic locations of the trained stimuli"? (If so, it should be cited.)

We added references supporting this assumption.

(6) Figure 2b: colorbar missing label.

We added the label.

Reviewer #2 (Recommendations for the authors):

Cool work!

(1) The reader would benefit from (a single) comprehensive figure that visually explains the entire conceptual framework-from TWCO principles to neural implementation to behavioural predictions-accessible to readers without specialised knowledge of oscillatory dynamics. This will give the paper a greater impact.

We have adjusted Figure 1 in accordance with suggestions made by reviewer 1 and added further explanations to the caption and the Introduction to enhance clarity on how the principles of TWCO relate to neural implementation.

(2) I think this paper would benefit from the audience eLife provides, but the paper could move closer to the audience.

(3) Pride comes before the fall, but I am not the most uninformed reader, and it took me some effort to process everything.

Thank you, we took this to heart. In the Introduction, we now state more explicitly how each variable is operationalized and how these map onto TWCO with improved reference to relevant panels in the schematic figure. We agree the framework is conceptually dense. TWCO principles reach the stimuli through specific V1 anatomy and physiology, so there are several links to keep in mind. Our goal with the revised introduction and figure is to make those links better visible.

(4) You could consider discussing potential implications for understanding perceptual disorders characterized by altered neural synchrony (e.g., schizophrenia, autism) and how your learning paradigm might inform perceptual training interventions.

Thank you for this suggestion. We have added that TWCO might provide a new lens to study perceptual disorders to the Discussion. We provide a concrete example of the relation between grouping, gamma synchrony (in light of TWCO) and lateral connectivity in schizophrenia

(5) I think this paper has real strength, but rather than dispersing limitations throughout the discussion, create a dedicated section that systematically addresses ecological validity, alternative explanations, and generalisability concerns. This will also preempt criticism.

We appreciate the suggestion. Our preference is to discuss limitations in context, next to the specific results they qualify, so readers see why each limitation matters and how it affects interpretation. Nevertheless, paragraph 7 on page 20 summarizes most limitations in a single paragraph.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer 1 (Public review):

When do behavioral differences emerge between the task variants? Based on the results and discussion, the cues increase the salience of either the wins or the losses, biasing behavior in favor of either risky or optimal choice. If this is the case, one might expect the cues to expedite learning, particularly in the standard and loss condition. Providing an analysis of the acquisition of the tasks may provide insight into how the cues are "teaching" decision-making and might explain how biases are formed and cemented.

While considerable differences in decision making emerge in early sessions of training, we do not observe any evidence that cuing outcomes expedites the development of stable choice patterns. Indeed, since the outcomes are cued across all four options, there is no categorical difference in salience between optimal and risky choices. Thus, our interpretation is that cuing wins and/or losses alters the integration of this feedback into choice preference, rather than the rate of the development of choice preference. To quantitatively address this point, we have included the following analysis:

“To quantitatively examine choice variability during training, we binned sessions 1-5 and 6-10 and analyzed variability in choice patterns across task variants. Analysis of the first five sessions of training revealed a significant shift in decision score across sessions (F(3, 502) = 31.23, p <.0001), which differed between task variants (session x task: F(16, 502) = 2.13, p = .007). Conversely, while significant differences in overall score were observed between task variants in sessions 6-10 (task: F(5, 156) = 6.81, p <.0001), there was no significant variability across sessions (session: F(3, 481) = 2.06, p = .10, task x session: F(15, 481) = 0.78, p = .71). This indicates that the variability in choice preference (and presumably, learning about outcomes) is maximized in the first five sessions, and there are no obvious differences in the rate of development of stable choice patterns between task variants.”

Does the learning period used for the modeling impact the interpretation of the behavioral results? The authors indicate that computational modeling was done on the first five sessions and used these data to predict preferences at baseline. Based on these results, punishment learning predicts choice preference. However, these animals are not naïve to the contingencies because of the forced choice training prior to the task, which may impact behavior in these early sessions. Though punishment learning may initially predict risk preference, other parameters later in training may also predict behavior at baseline.

The first five sessions were chosen based on a previously developed method used in Langdon et al. (2019). When choosing the number of sessions to include, there is a balance between including more data points to improve estimation of parameters while also targeting the timeframe of maximal learning. As training continues, the impact of outcomes on subsequent choice should decrease, and the learning rate would trend towards zero. This can be observed in the reduction in inter-session choice variability as training progresses, as demonstrated in the analyses above. Once learning has ceased, presumably other cognitive processes may dictate choice (for example, habitual stimulus-response associations), which would not be appropriately captured by reinforcement learning models. It would be a separate research question to determine the point at which parameters no longer become predictive, requiring a larger dataset to thoroughly assess. We acknowledge that we did not provide sufficient justification for the learning period used for the modeling. In conjunction with the analysis of early sessions outlined above, we have added the following to the text:

“We investigated differences in the acquisition of each task variant by fitting several reinforcement learning (RL) models to early sessions. Our modeling approach closely follows methods outlined in Langdon et al. (2019), in which a much larger dataset (>100 rats per task) was used to develop the RL models applied here. Due to the comparatively small n per group in the current study, we limited our model selection to those previously validated in Langdon et al. (2019), with minor extensions. As in previous work, models were fit to valid choices from the first five sessions. As training continues, the impact of outcomes on subsequent choice should decline, and parameter values may evolve over time (e.g., decreasing learning rate). To target the period of learning during which outcomes have maximal influence over choice, and parameters likely have fixed values, we limited our analyses to the first five sessions.”

The authors also present simulated data from the models for sessions 18-20, but according to the statistical analysis section, sessions 35-40 were used for analysis (and presumably presented in Figure 1). If the simulation is carried out in sessions 35-40, do the models fit the data?

Based on our experience, choice patterns are well instantiated by session 20, and training only continues to 30+ sessions to achieve stability in other task variables (e.g., latencies, premature responding, etc.). That being said, the discrepancy between session numbers is confusing, so we’ve extended the simulations to match the same session numbers that were analyzed in the experimental data.

Finally, though the n's are small, it would be interesting to see how the devaluation impacts computational metrics. These additional analyses may help to explain the nuanced effects of the cues in the task variants. 

Unfortunately, as the devaluation experiment is only one session, there are insufficient data to run the same models. Furthermore, changes in choice are subtle and not uniform across rats, making it difficult to reliably model this effect at the individual level. A separate experiment could investigate the specific cognitive processes underlying the devaluation effect.

Reviewer #1 (Recommendations for the authors):

The authors do not present individual data points for behavior. Including these data points would improve the interpretability of the results. Adding significant notations to the bar graphs would also help the reader. Although the stats are provided and significant comparisons highlighted, it isn't easy to go between the table and the figure to detect significant outcomes. If done, the statistics tables could be moved to the supplement. Including estimates of effect size for main findings in the main text would also benefit the reader. 

We thank the reviewer for their feedback on our approach to the figures and significance reporting – we have updated the relevant figures to include individual data points. Furthermore, we’ve added significance notations for task variants that are significantly different from the uncued or standard cued tasks on the figures. We’ve also moved some statistics tables to the supplement, as suggested. 

The authors allude to other metrics of the task (trials, omissions, etc.) but do not present these data anywhere. Including supplementary figures including individual data points and statistical analyses in the supplement is strongly encouraged.

A supplementary figure visualizing these metrics (choice latency, trials completed, and omissions) has been added, with individual data points included. Statistical analyses are reported in the main text – no significant effect in the ANOVAs were observed for any of these metrics, so post hoc analyses were not performed. 

Figure 4 is confusing. Presenting the WAIC values for each model rather than compared to the nonlinear model would be easier to understand. It is also unclear if statistical tests were used to assess differences in model fit as no test information is provided.

Figure 4 has been updated to increase clarity and address feedback from another reviewer. Raw WAIC values are not ideal for visualization, as the task variants have differing amounts of data and thus would be difficult to include on the same Y-axis. Instead, we present each model’s difference in WAIC relative to a basic model with no timeout penalty transform, so that all three models are visible, and the direction of model improvement is clearly indicated. Statistical tests of WAIC differences are not standard, as the numerical differences themselves indicate a better fit.

The authors do not provide a data availability statement.

We thank the reviewer for calling our attention to this oversight. A data availability statement has been added. 

Reviewer 2 (Public review):

Additional support and evidence are needed for the claims made by the authors. Some of the statements are inconsistent with the data and/or analyses or are only weakly supportive of the claims.

We appreciate the reviewer’s overarching concern that some claims in the original manuscript were insufficiently supported by the data or analyses. To address this, we have provided further rationale for the devaluation experiment and clarified our interpretation of those results, expanded the computational modeling analyses, and revised figures and wording to improve clarity. Below, we respond to the reviewer’s specific comments in detail.

Reviewer #2 (Recommendations for the authors):

Different variants of an RL model were used to understand how loss outcomes impacted choice behavior across the gambling task variants. Did the authors try different variants for rewarded outcomes? I wonder whether the loss specific RL effects are constrained to that domain or perhaps emerged because choice behavior to losses was better estimated with the different RL variants. For example, rewarded outcomes across the different choices may not scale linearly (e.g., 1, 2, 3, 4) so including a model in which Rtr is scaled by a free parameter might improve the fit for win choices.

We agree that asymmetries in model flexibility could, in principle, contribute to the observed effects. While we are somewhat limited in our ability to develop and validate further models due to the small size of the datasets compared to the high degree of choice variability between rats, we have explored the possibility as far as the data allow by fitting a model that includes a scaling parameter for rewards in addition to punishments:

“While we restricted our model selection to those previously validated on larger datasets, the specificity of the main finding to the punishment learning rate may be due to the greater flexibility afforded to loss scaling, rather than a true asymmetry in learning. To test this hypothesis, we fit a model featuring a scaling parameter for rewards, in addition to scaled costs:

where mRew is a linear scaling parameter for reward size. A separate scaling parameter was used for timeout penalty duration (i.e., same as scaled cost model). Group-level parameter estimates (Figure S3) reflected similar differences in the punishment learning rate and reward learning rate as the scaled cost model (Figure S4). Furthermore, all 95% HDIs for the mRew scaling parameter included 1, indicating that at least at the group level, scaling of reward size across the P1-P4 options closely follows the actual number of earned sucrose pellets. Thus, we find no evidence that our results can be simply attributed to the increased parameterization of losing outcomes.”

Additionally, I would like to see evidence that these alternative models provide a better fit compared to a standard delta-rule updating for unrewarded choices.

Each model is now compared directly to a standard delta-rule update model in the WAIC figure to demonstrate that the current models are a better fit for the data.

Could the authors provide some visualization of how variation in the r, m, or b parameters impact choices and/or patterns of choices?

We have added a figure to the supplementary section to visualize how different values for the r, m, and b parameters could alter the size of updates to Q-values on each trial across the four different options, thereby impacting subsequent choice. 

It was challenging to understand the impact of the reported effects and interpretation of the authors at various points in the manuscript. For example, the authors state that "only rats trained on tasks without win-paired cues exhibited shifts in risk preference following reinforcer devaluation". Figure 3 however seems to indicate that rats trained on the reverse-cued task show shifts in risk preference. 

We agree the original wording did not fully capture the nuance apparent in the figure. While not significantly different from baseline, rats in the reverse-cued experiment could have indeed updated their choice patterns and we were underpowered to detect the effect. We have updated the results section to include this point, and to more specifically outline that win-paired cues that scale with reward size lead to insensitivity to reinforcer devaluation:

“This indicates that pairing audiovisual cues with reward induces some degree of inflexibility in risk-preferring rats. Importantly, pairing cues with losses alone does not elicit rigidity in choice. Thus, in keeping with the observed effect on overall choice patterns, pairing cues with wins has a unique impact on sensitivity to reinforcer devaluation. Although not statistically significant, visual inspection of the reverse-cued task suggests that some choice flexibility may be present, and the study may be underpowered to detect this effect. Nonetheless, win-paired cues that scale with reward size reduce flexibility in choice patterns following reinforcer devaluation.”

It was not clear to me why the authors did a devaluation test and what was expected. Adding details regarding the motivation for specific analyses and/or experiments would improve understanding of these exciting results.

Further explanation has been added to the results section for the devaluation test to clarify the rationale and expected results:

“We next tested whether pairing salient audiovisual cues with outcomes on the rGT impacts flexibility in decision making when outcome values are updated. Reinforcer devaluation, in which subjects are sated on the sugar pellet reinforcer prior to task performance (presumably devaluing the outcome), is a common test of flexibility of decision making (Adams & Dickinson, 1981). We have previously employed this method to demonstrate that rats trained on the standard-cued task are insensitive to reinforcer devaluation (i.e., choice patterns do not shift despite devaluation of the sugar pellet reward; Hathaway et al., 2021).”

Some rats in the rGT become risk takers and some do not, but whether this is an innate phenomenon or emerges with training is not known. The authors report some correlations between the RL parameters and subsequent risk scores but this may be an artifact because the risk scores and many of the parameters differ between the experimental groups. Restricting these analyses to the rats in the standard procedure (or even conducting it in other rats that have been run in the rGT standard task) would alleviate this concern. The authors should also expand upon this result in the discussion. (if it holds up) and provide graphs of this relationship in the manuscript.

In a previous paper on which these analyses were based (Langdon et al., 2019), analyses of the relationship between RL parameter estimates and final decision score were conducted separately for rats trained on either the uncued or standard cued task, as the reviewer has suggested here. Those analyses showed that parameters controlling the learning from negative outcomes were specifically related to final score in both tasks. While we don’t have the appropriate n per group to split the analyses by task variant in the current study, we have highlighted these previous findings in the results section to address this concern:

“In Langdon et al. (2019), analyses were conducted to test whether parameters controlling sensitivity to punishment predicted final decision score at the end of training in the uncued and standard cued task variants. These analyses showed that across both task variants, there was evidence of reduced punishment sensitivity (i.e., lower m parameter or punishment learning rate) in risky versus optimal rats. We conducted similar analyses here to examine whether parameter estimates covary with decision score at end of training. To accomplish this, we fit simple linear regression models for each parameter and assessed whether the slopes were significantly different from zero.”

I don't see a b parameter in the nonlinear cost model, but is presented in Figure 6 and also in the "Parameters predicting risk preference on the rGT". The authors either need to update the formula or clarify what the b parameter quantifies in the nonlinear model.

We thank the reviewer for pointing out this oversight; the equation has been updated to include the b parameter.

The risk score is very confusing as high numbers or % indicate less risk and lower (more negative numbers) indicate greater risk. I've had to reread the text multiple times to remind myself of this, so I anticipate the same will be true for other readers. Perhaps the authors can add a visual guide to their y-axis indicating more positive numbers are less risky choices.

We acknowledge that this measure can be confusing – the calculation of this score is standard for the Iowa Gambling Task conducted in humans, on which the rGT is based, and was therefore adopted here. We’ve changed the name from “risk score” to “decision score”, along with including a visual guide to the y-axis in Figure 2, to address this point.

Negative learning rate is confusing as it almost implies that the learning was a negative value, rather than being a learning rate for negative outcomes. Please revise in the figures and in the text.

We have updated the text and figures where appropriate from “negative learning rate” to “punishment learning rate”. We have also changed the text from “positive learning rate” to “reward learning rate” to match this terminology.

Reviewer 3 (Public review):

There is a very problematic statistical stratagem that involves categorising individuals as either risky or optimal based on their choice probabilities. As a measurement or outcome, this is fine, as previously highlighted in the results, but this label is then used as a factor in different ANOVAs to analyse the very same choice probabilities, which then constitutes a circular argument (individuals categorised as risky because they make more risky choices, make more risky choices...).

Risk status was included as a factor to test whether the effects of the cue paradigms differed between risky versus optimal rats (i.e., interaction effects), not as an independent predictor of choice preference. We focus on results showing a significant task x risk status interaction, and conducted follow-up analyses separately within each group, at which point risk status was no longer included as a factor. We do not interpret main effects or choice x status interactions, which would indeed be circular for the reason noted by the reviewer.

A second experiment was done to study the effect of devaluation on risky choices in the different tasks. The results, which are not very clear to understand from Figure 3, would suggest that reward devaluation affects choices in tasks where the win-cue pairing is not present. The authors interpret this result by saying that pairing wins with cues makes the individuals insensitive to reward devaluation. Counter this, if an individual is prone to making risky choices in a given task, this points to an already distorted sense of value as the most rewarding strategy is to make optimal non-risky choices.

We have included significance notations in Figure 3 and included further detail in the text to improve clarity of the findings for the devaluation test. The reviewer raises an interesting point that risk-preferring rats have a distorted sense of value, since they do not follow the optimal strategy. However, we believe that this is at least partially separable from insensitivity to devaluation, since risk-preferring rats trained on tasks that don’t feature win-paired cues still exhibit flexibility in choice. We have added the following point to the discussion to address this:

“While risk-preferring rats exhibit some degree of distortion in reward valuation, as they do not follow the most rewarding strategy (i.e., selecting optimal options), we believe this to be at least partially separable from choice inflexibility, as risk-preferring rats on tasks that don’t feature win-paired cues remain sensitive to devaluation.”

While the overall computational approach is excellent, I believe that the choice of computational models is poor. Loss trials come at a double cost, something the authors might want to elaborate more upon, firstly the lost opportunity of not having selected a winning option which is reflected in Q-learning by the fact that r=0, and secondly a waiting period which will affect the overall reward rate. The authors choose to combine these costs by attempting to convert the time penalty into "reward currency" using three different functions that make up the three different tested models. This is a bit of a wasted opportunity as the question when comparing models is not something like "are individuals in the paired win-cue tasks more sensitive to risk? or less sensitive to time? etc" but "what is the best way of converting time into Q-value currency to fit the data?" Instead, the authors could have contrasted other models that explicitly track time as a separate variable (see for example "Impulsivity and risk-seeking as Bayesian inference under dopaminergic control" (Mikhael & Gershman 2021)) or give actions an extra risk bonus (as in "Nicotinic receptors in the VTA promote uncertainty seeking" (Naude et al 2016)).

We thank the reviewer for their thoughtful suggestions and agree that alternative modeling frameworks that explicitly track time or incorporate uncertainty bonuses would be highly informative for understanding the mechanisms underlying risky choice. However, the models employed here are drawn from previous work that required >100 rats per group for model development and validation. Due to the high degree of variability in decision making within the groups and the relatively small number of rats, this dataset is not well suited for substantial model innovation. Indeed, the most complex model from previous work had to be simplified to achieve model convergence. Testing models that greatly diverge from the previously validated RL models would make it difficult to determine whether poor model fit reflects a misspecified model or insufficient data.

We’d also like to note that the driving question for this study is to investigate the impact of different cue variants on choice patterns – untangling the relationship between timing, uncertainty, and risky choice is an important and interesting question, but beyond the scope of the present work. 

To address this limitation, we have expanded our justification of model choice in the results section to emphasize that we are applying previously developed models, with minor extensions:

“We investigated differences in the acquisition of each task variant by fitting several reinforcement learning (RL) models to early sessions. Our modeling approach closely follows methods outlined in Langdon et al. (2019), in which a much larger dataset (>100 rats per task) was used to develop the RL models applied here. Due to the comparatively small n per group in the current study, we limited our model selection to those previously validated in Langdon et al. (2019), with minor extensions.”

Another weakness of the computational section is the fact, that despite simulations having been made, figure 5 only shows the simulated risk scores and not the different choice probabilities which would be a much more interesting metric by which to judge model validity. 

We have expanded Figure 5 to show the simulated choice of each option.

In the last section, the authors ask whether the parameter estimates (obtained from optimisation on the early sessions) could be used to predict risk preference. While this is an interesting question to address, the authors give very little explanation as to how they establish any predictive relationship. A figure and more detailed explanation would have been warranted to support their claims.

We have expanded this section to provide clearer detail on the methods used to conduct this analysis and added a figure. To address a point raised by another reviewer, the statistical approach has been revised to more closely align with that used in Langdon et al. (2019), and the results have been updated appropriately:

“We next tested whether any of the subject-level parameter estimates in the nonlinear or scaled + offset model could reliably predict risk preference scores at the end of training. In Langdon et al. (2019), analyses were conducted to test whether parameters controlling sensitivity to punishment predicted final decision score at the end of training in the uncued and standard cued task variants. These analyses showed that across both task variants, there was evidence of reduced punishment sensitivity (i.e., lower m parameter or punishment learning rate) in risky versus optimal rats. We conducted similar analyses here to examine whether parameter estimates covary with decision score at end of training. To accomplish this, we fit simple linear regression models for each parameter and assessed whether the slopes were significantly different from zero.”

Why were the simulated risk scores calculated for sessions 18-20 and not 35-39 as in the experimental data, and why were the models optimised only on the first sessions?

These points were addressed in response to reviewer #1:

Based on our experience, choice patterns are well instantiated by session 20, and training only continues to 30+ sessions to achieve stability in other task variables (e.g., latencies, premature responding, etc.). That being said, the discrepancy between session numbers is confusing, so we’ve extended the simulations to match the same session numbers that were analyzed in the experimental data.

The first five sessions were chosen based on a previously developed method used in Langdon et al. (2019). When choosing the number of sessions to include, there is a balance between including more data points to improve estimation of parameters while also targeting the timeframe of maximal learning. As training continues, the impact of outcomes on subsequent choice should decrease, and the learning rate would trend towards zero. This can be observed in the reduction in inter-session choice variability as training progresses, as demonstrated in the analyses above. Once learning has ceased, presumably other cognitive processes may dictate choice (for example, habitual stimulus-response associations), which would not be appropriately captured by reinforcement learning models. It would be a separate research question to determine the point at which parameters no longer become predictive, requiring a larger dataset to thoroughly assess. We acknowledge that we did not provide sufficient justification for the learning period used for the modeling. In conjunction with the analysis of early sessions outlined above, we have added the following to the text:

“We investigated differences in the acquisition of each task variant by fitting several reinforcement learning (RL) models to early sessions. Our modeling approach closely follows methods outlined in Langdon et al. (2019), in which a much larger dataset (>100 rats per task) was used to develop the RL models applied here. Due to the comparatively small n per group in the current study, we limited our model selection to those previously validated in Langdon et al. (2019), with minor extensions. As in previous work, models were fit to valid choices from the first five sessions. As training continues, the impact of outcomes on subsequent choice should decline, and parameter values may evolve over time (e.g., decreasing learning rate). To target the period of learning during which outcomes have maximal influence over choice, and parameters likely have fixed values, we limited our analyses to the first five sessions.”

Concerning the figures, could you consider replacing or including with the bar plots, the full distribution of individual dots, or a violin plot, something to better capture the distribution of the data. This would be particularly beneficial for Figure 2B the risk score which, without a distribution suggests all individuals are optimal, something which in the text claim is not the case. 

Individual data points have been added to the relevant figures.

Is this not a case of compositional data where ANOVA is definitely not an appropriate method (compositional data consist in reporting proportions of different elements in a whole, eg this rock is 60% silicate, 20% man-made cement, etc.) because of violation of normality and mostly dependence between measurements (the sum must be 100% as in your case where knowing the proportions of P1, P2 and P3, I automatically deduce P4). I leave to you the care of finding a potential alternative. In any case, I also had difficulties understanding the varying degrees of freedom of the different reported F statistics which worry me that this has not been done properly.

This is a fair criticism, as choice proportions across P1-P4 are not fully independent. While alternative approaches do exist, there is no widely adopted or straightforward method that has been validated for this task. Accordingly, ANOVA remains the standard analytical approach for this task, as it facilitates comparison with previous work and is readily understood by readers. As mentioned in the methods, an arcsine transformation was applied to the proportional data to mitigate issues associated with bounded measures (i.e., summing to 100%). We thank the reviewer for drawing our attention to the discrepancies in the degrees of freedom – these have now been corrected.

Author response:

The following is the authors’ response to the original reviews

eLife Assessment

This study provides a useful analysis of the changes in chromatin organization and gene expression that occur during the differentiation of two cell types (anterior endoderm and prechordal plate) from a common progenitor in zebrafish. Although the findings are consistent with previous work, the evidence presented in the study appears to be incomplete and would benefit from more rigorous interpretation of single-cell data, more in-depth lineage tracing, overexpression experiments with physiological levels of Ripply, and a clearer justification for using an explant system. With these modifications, this paper will be of interest to zebrafish developmental biologists investigating mechanisms underlying differentiation.

We sincerely thank the editor and the reviewers for their valuable time and efforts. Their insightful comments were greatly appreciated and have been largely addressed in the revised manuscript. We are confident that these revisions have enhanced the overall quality and clarity of our paper.

Reviewer #1 (Public review):

Summary:

During vertebrate gastrulation, mesendoderm cells are initially specified by morphogens (e.g. Nodal) and segregate into endoderm and mesoderm in part based on Nodal concentrations. Using zebrafish genetics, live imaging, and single-cell multi-omics, the manuscript by Cheng et al presents evidence to support a claim that anterior endoderm progenitors derive primarily from prechordal plate progenitors, with transcriptional regulators goosecoid (Gsc) and ripply1 playing key roles in this cell fate determination. Such a finding would represent a significant advance in our understanding of how anterior endoderm is specified in vertebrate embryos.

We would like to thank reviewer #1 for his/her comments and positive feedbacks about our manuscript.

Strengths:

Live imaging-based tracking of PP and endo reporters (Figure 2) is well executed and convincing, though a larger number of individual cell tracks will be needed. Currently, only a single cell track (n=1) is provided.

We thank the reviewer for the positive comments and the valuable suggestion. As the reviewer suggested, we re-performed live imaging analyses on the embryos of Tg(gsc:EGFP;sox17:DsRed). We tracked dozens of cells during their transformation from gsc-positive to sox17-positive. Furthermore, we performed quantification of the RFP/GFP signal intensity ratio in these cells over the course of development (Please see the revised Figure 2D and MovieS4).

Weaknesses:

(1) The central claim of the paper - that the anterior endoderm progenitors arise directly from prechordal plate progenitors - is not adequately supported by the evidence presented. This is a claim about cell lineage, which the authors are attempting to support with data from single-cell profiling and genetic manipulations in embryos and explants. The construction of gene expression (pseudo-time) trajectories, while a modern and powerful approach for hypothesis generation, should not be used as a substitute for bona fide lineage tracing methods. If the authors' central hypothesis is correct, a CRE-based lineage tracing experiment (e.g. driving CRE using a PP marker such as Gsc) should be able to label PP progenitor cells that ultimately contribute to anterior endoderm-derived tissues. Such an experiment would also allow the authors to quantify the relative contribution of PP (vs non-PP) cells to the anterior endoderm, which is not possible to estimate from the indirect data currently provided. Note: while the present version of the manuscript does describe a sox17:CRE lineage tracing experiment, this actually goes in the opposite direction that would be informative (sox:17:CRE-marked descendants will be a mixture of PP-derived and non-PP derived cells, and the Gsc-based reporter does not allow for long-term tracking the fates of these cells).

We sincerely thank the reviewer for the professional comments and the constructive suggestions. As the reviewer indicated, utilizing the single-cell transcriptomic trajectory analyses on zebrafish embryos and Nodal-injected explants system, along with the live imaging analyses on Tg(gsc:EGFP;sox17:DsRed) embryos, we revealed that anterior endoderm progenitors arise from prechordal plate progenitors. To further verify this observation, we conducted two sets of lineage-tracing assays. Initial evidence came from the results of co-injecting sox17:Cre and gsc:loxp-STOP-loxp-mcherry plasmids. We observed RFP-positive cells at 8 hpf, demonstrating the presence of cells that had expressed both genes. To explicitly follow the proposed lineage, we then implemented a reciprocal strategy, as suggested by the reviewer, that constructed and co-injected sox17:loxp-STOP-loxp-mcherry and gsc:Cre plasmids. The appearance of RFP-positive cells in the anterior dorsal region at 8 hpf provides direct evidence for a transition from gsc-positive to sox17-positive identity. These results are now included in the revised manuscript (Please see Author response image 1 and Figure S4E). However, in accordance with the reviewer's caution, we acknowledge that this does not prove this is the sole origin of anterior endoderm. Consequently, we have revised the text to clarify that our findings demonstrate that anterior endoderm can be specified from prechordal plate progenitors, without claiming that it is the only source.

Author response image 1.

Characterization of anterior endoderm lineage by Cre-Lox recombination system.

(2) The authors' descriptions of gene expression patterns in the single-cell trajectory analyses do not always match the data. For example, it is stated that goosecoid expression marks progenitor cells that exist prior to a PP vs endo fate bifurcation (e.g. lines 124-130). Yet, in Figure 1C it appears that in fact goosecoid expression largely does not precede (but actually follows) the split and is predominantly expressed in cells that have already been specified into the PP branch. Likewise, most of the cells in the endo branch (or prior) appear to never express Gsc. While these trends do indeed appear to be more muddled in the explant data (Figure 1H), it still seems quite far-fetched to claim that Gsc expression is a hallmark of endoderm-PP progenitors.

We thank the reviewer for pointing out this issue. Our initial analysis proposed that the precursors of the prechordal plate (PP) and anterior endoderm (endo) more closely resemble a PP cell fate, as their progenitor populations highly express PP marker genes, such as gsc. The gsc gene is widely recognized as a PP marker[1]. The reviewer pointed out that in our analysis, these precursor cells do not initially exhibit high gsc expression; rather, gsc expression gradually increases as PP fate is specified.

The reason for this observation is as follows: First, for the in vivo data, we used the URD algorithm to trace back all possible progenitor cells for both the PP and anterior endo trajectory. As mentioned in the manuscript, the PP and anterior endo are relatively distant in the trajectory tree of the zebrafish embryonic data. Consequently, this approach likely included other, confounding progenitor cells that do not express gsc (like ventral epiblast, Author response image 2). However, we further investigated the expression of gsc and sox17 along these two trajectories. The conclusion remains that gsc expression is indeed higher than sox17 in the progenitor cells common to both trajectories (Author response image 2). Combined with the live imaging analysis presented in this study, which shows that gsc expression increases progressively in the PP, this supports the notion that the progenitor cells for both PP and anterior endoderm initially bias towards a PP cell fate.

On the other hand, in our previously published work using the Nodal-injected explant system, which specifically induces anterior endo and PP, the cellular trajectory analysis also revealed that the specifications of PP and anterior endo follow very similar paths. Therefore, we proceeded to analyze the Nodal explant data. Similarly, when using URD to trace the differentiation trajectories of PP and anterior endo cells, a small number of other progenitor cells were also captured. This explains why a minority of cells do not express gsc—these are likely ventral epiblast cells (Author response image 2). However, based on the Nodal explant data, gsc is specifically highly expressed in the progenitor cells of the PP and anterior endo. Its expression remains high in the PP trajectory but gradually decreases in the endoderm trajectory (Figure 1H).

Author response image 2.

(A) The expression of ventral epiblast markers in PP and anterior Endo URD trajectory. (B) The expression of gsc, sox32 and sox17 in the progenitors of PP and anterior endo in embryos and Nodal explants.

(3) The study seems to refer to "endoderm" and "anterior endoderm" somewhat interchangeably, and this is potentially problematic. Most single-cell-based analyses appearing in the study rely on global endoderm markers (sox17, sox32) which are expressed in endodermal precursors along the entire ventrolateral margin. Some of these cells are adjacent to the prechordal plate on the dorsal side of the gastrula, but many (most in fact) are quite some distance away. The microscopy-based evidence presented in Figure 2 and elsewhere, however, focuses on a small number of sox17-expressing cells that are directly adjacent to, or intermingled with, the prechordal plate. It, therefore, seems problematic for the authors to generalize potential overlaps with the PP lineage to the entire endoderm, which includes cells in ventral locations. It would be helpful if the authors could search for additional markers that might stratify and/or mark the anterior endoderm and perform their trajectory analysis specifically on these cells.

We thank the reviewer for these comments and suggestions. We fully agree with the reviewer's point that the expression of sox32 and sox17 cannot be used to distinguish dorsal endoderm from ventral-lateral endoderm cells. However, during the gastrulation stage, all endodermal cells express sox32 and sox17, and there are currently no specific marker genes available to distinguish between them.

After gastrulation ends, the dorsal endoderm (i.e., the anterior endoderm) begins to express pharyngeal endoderm marker genes, such as pax1b. Therefore, in the analysis of embryonic data in vivo, when studying the segregation of the anterior endoderm and PP trajectory, we specifically used the pharyngeal endoderm as the subject to trace its developmental trajectory.

In the case of Nodal explants, Nodal specifically induces the fate of the dorsal mesendoderm, which includes both the PP and pharyngeal endoderm (anterior endoderm). Precisely for this reason, we consider the Nodal explant system as a highly suitable model for investigating the mechanisms underlying the cell fate separation between anterior endoderm and PP. Thus, in the Nodal explant data, we included all endodermal cells for downstream analysis.

To avoid any potential confusion for readers, we have revised the term "endoderm" in the manuscript to "anterior endoderm" as suggested by the reviewer.

(4) It is not clear that the use of the nodal explant system is allowing for rigorous assessment of endoderm specification. Why are the numbers of endoderm cells so vanishingly few in the nodal explant experiments (Figure 1H, 3H), especially when compared to the embryo itself (e.g. Figures 1C-D)? It seems difficult to perform a rigorous analysis of endoderm specification using this particular model which seems inherently more biased towards PP vs. endoderm than the embryo itself. Why not simply perform nodal pathway manipulations in embryos?

We sincerely thank the reviewer for raising this important question. In our study of the fate separation between the PP and anterior endoderm, we initially analyzed zebrafish embryonic data. However, when reconstructing the transcriptional lineage tree using URD, we observed that these two cell trajectories were positioned relatively far apart on the tree. Yet, existing studies have shown that the anterior endoderm and PP are not only spatially adjacent but also both originate from mesendodermal progenitor cells[2-4], and they share transcriptional similarities[5]. Therefore, as the reviewer pointed out, when tracing all progenitor cells of these two trajectories using the URD algorithm, it is easy to include other cell types, such as ventral epiblast cells (Author response image 2). For this reason, we concluded that directly using embryonic data to dissect the mechanism of fate separation between PP and anterior endoderm might not yield highly accurate results.

In contrast, our group’s previous work, published in Cell Reports, demonstrated that the Nodal-induced explant system specifically enriches dorsal mesendodermal cells, including anterior endoderm, PP, and notochord[5]. Thus, we considered the Nodal explant system to be a highly suitable model for investigating the mechanism of fate separation between PP and anterior endoderm. Ultimately, by analyzing both in vivo embryonic data and Nodal explant data, we consistently found that the anterior endoderm likely originates from PP progenitor cells—a conclusion further validated by live imaging experiments.

Regarding the reviewer’s concern about the relatively low number of endodermal cells in the Nodal explant system, we speculate that this is because the explants predominantly induce anterior endoderm. Since endodermal cells constitute only a small proportion of cells during gastrulation, and anterior endoderm represents an even smaller subset, the absolute number is naturally limited. Nevertheless, the anterior endodermal cells captured in our Nodal explants were sufficient to support our analysis of the fate separation mechanism between anterior endoderm and PP. Finally, to further strengthen the findings from scRNA-seq analyses, we subsequently performed live imaging validation experiments using both zebrafish embryos and the explant system.

(5) The authors should not claim that proximity in UMAP space is an indication of transcriptional similarity (lines 207-208), especially for well-separated clusters. This is a serious misrepresentation of the proper usage of the UMAP algorithm. The authors make a similar claim later on (lines 272-274).

We would like to extend our gratitude to the reviewer for their insightful comments. We have revised the descriptions regarding UMAP throughout the manuscript as suggested (Please see the main text in revised manuscript).

Reviewer # 1 (Recommendations For The Authors):

- Pseudotime trajectories constructed from single-cell snapshots are not true "lineage" measurements. Authors should refrain from referring to such data as lineage data (e.g. lines 99, 100, 103, 109, 112, 127, etc). Such models should be referred to as "trajectories", "hypothetical lineages", or something else.

We are grateful to the reviewer for this comment. Following their recommendation, we have revised the terminology from "transcriptional lineage tree" to "trajectory" across the entire manuscript (Please see main text in revised manuscript).

- The live imaging data presented in Figure 2 (and supplemental figures) are compelling and do seem to show that some cells can switch between PP and endo states. However, the number of cells reported is still too low to be able to ascertain whether or not this is just a rare/edge-case phenomenon. Tracks for just a single cell are reported in Figure 2C-D. This is insufficient. Tracks for many more cells should be collected and reported alongside this current sole (n=1) example. The choice of time window for these live imaging experiments should also be better explained. These live imaging experiments are being performed at or after 6hpf, but authors claim in the text that "... the segregation between PP and Endo has already occurred by 6hpf." (lines 126-127). Why not perform these live imaging experiments earlier, when the initial fate decision between PP and endo is supposedly occurring?

We sincerely appreciate the reviewer’s insightful questions and constructive feedback. In response, we have made several important revisions. First, the reviewer noted that our original manuscript tracked only a single cell and suggested increasing the number of tracked cells. Following this recommendation, we repeated the live-imaging experiments and expanded the number of tracked endodermal cells (Please see the revised Movie S4 and Figure 2D). The experimental conditions were kept identical to the previous setup, and these cells consistently exhibited a gradual transition from a gsc+ fate to a sox17+ endodermal fate. In addition, the reviewer recommended performing live imaging at an earlier time point (Movie S5). Accordingly, we conducted additional experiments initiating live imaging at around 5.7 hours and observed the onset of a sox17 expression in gsc+ cells at approximately 6 hpf, which is consistent with our single-cell transcriptomic analysis.

- The sections devoted to lengthy descriptions of GO terms (lines 131-146, 239-254) and receptor-ligand predictions (lines 170-185) are largely speculative. Consider streamlining.

Thanks for the reviewer's comment. We have streamlined the content related to the GO analysis as suggested (Please see Lines 128-132, 157-167, 221-225).

- The use of a "Nodal Activity Score" (lines 212-226) is clever but might actually be less informative than showing contributions from individual nodal target genes. The combining of counts data from 29 predicted nodal targets means that the contribution (or lack of contribution) from each gene becomes masked. The authors should include supplementary dot plots that break down the score across all 29 genes, allowing the reader to assess overall contributions and/or sub-clusters of gene co-expression patterns, if present.

Thank you very much for the reviewer's positive feedback on our use of the "Nodal Activity Score" and the valuable suggestions provided. Following the recommendation, we analyzed the expression of the 29 Nodal direct targets used in our study across the WT, ndr1 knockdown (kd), and lft1 knockout (ko) groups. We found that the known axial mesoderm genes, such as chrd, tbxta, noto, and gsc, contributed significantly to the Nodal score. The newly conducted analysis has been included in the Supplementary Information (Please see Figure S7L).

- The differential expression trends being reported for srcap (line 251) do not appear to be significant. Are details and P-values for these DEG tests reported somewhere in the manuscript?

We thank the reviewer for raising this question. Based on the reviewer's comment, we performed statistical tests (Wilcoxon test) to compare the expression of srcap in PP and Endo. Our analysis revealed that while srcap expression is slightly higher in PP than in Endo, this difference is not statistically significant. The specific p-value and fold change have been indicated in the revised figure (Please see Figure 4J and S7H). Based on this analysis, we revised our description to state that srcap expression is slightly higher in the PP compared to in the anterior endoderm.

- Following the drug experiments with the drug AU15330 (lines 254-263), authors have only reported #s of endodermal cells, which seem to have increased, which the authors suggest indicates a fate switch from PP to endo. However, the authors have not reported whether the numbers of PP cells decreased or stayed the same in these embryos. This would be helpful information to include, as it is very difficult to discern quantitative trends from the images presented in Fig 4H and 4L.

Thank the reviewer for his/her comments and suggestions. Following the reviewer's suggestions, we performed Imaris analysis on the HCR staining results from the DMSO (control), 1μM AU15330-treated, and 5μM AU15330-treated groups. Our analysis focused on the number of frzb-positive cells (PP), and the comparison revealed that treatment with AU15330 significantly reduces the PP cell number. These findings have been incorporated into the revised manuscript and supplementary information (Please see Figures S7J and S7K).

Reviewer #2 (Public review):

Summary:

During vertebrate gastrulation, the mesoderm and endoderm arise from a common population of precursor cells and are specified by similar signaling events, raising questions as to how these two germ layers are distinguished. Here, Cheng and colleagues use zebrafish gastrulation as a model for mesoderm and endoderm segregation. By reanalyzing published single-cell sequencing data, they identify a common progenitor population for the anterior endoderm and the mesodermal prechordal plate (PP). They find that expression levels of PP genes Gsc and ripply are among the earliest differences between these populations and that their increased expression suppresses the expression of endoderm markers. Further analysis of chromatin accessibility and Ripply cut-and-tag is consistent with direct repression of endoderm by this PP marker. This study demonstrates the roles of Gsc and Ripply in suppressing anterior endoderm fate, but this role for Gsc was already known and the effect of Ripply is limited to a small population of anterior endoderm. The manuscript also focuses extensively on the function of Nodal in specifying and patterning the mesoderm and endoderm, a role that is already well known and to which the current analysis adds little new insight.

We would like to thank the reviewer #2 for the constructive comments and positive feedback regarding our manuscript.

Strengths:

Integrated single-cell ATAC- and RNA-seq convincingly demonstrate changes in chromatin accessibility that may underlie the segregation of mesoderm and endoderm lineages, including Gsc and ripply. Identification of Ripply-occupied genomic regions augments this analysis. The genetic mutants for both genes provide strong evidence for their function in anterior mesendoderm development, although these phenotypes are subtle.

We thank the reviewer for recognizing our work, and we greatly appreciate the constructive suggestions from the reviewer.

Weaknesses:

The use of zebrafish embryonic explants for cell fate trajectory analysis (rather than intact embryos) is not justified. In both transcriptomic comparisons between the two fate trajectories of interest and Ripply cut-and-tag analysis, the authors rely too heavily on gene ontology which adds little to our functional understanding. Much of the work is focused on the role of Nodal in the mesoderm/endoderm fate decision, but the results largely confirm previous studies and again provide few new insights. Some experiments were designed to test the relationship between the mesoderm and endoderm lineages and the role of epigenetic regulators therein, but these experiments were not properly controlled and therefore difficult to interpret.

We sincerely thank the reviewer for the comments. As we previously answered, in our study of the fate differentiation between the PP and the anterior endoderm, we initially analyzed zebrafish embryonic data. However, when we used URD to reconstruct the transcriptional trajectory tree, we found that these two cell trajectories were distantly located on the tree. Existing studies have shown that the anterior endoderm and the PP are not only spatially adjacent but also both originate from mesendodermal progenitor cells and share transcriptional similarities[2-4]. Therefore, when tracing all progenitor cells of these two trajectories using the URD algorithm, it is easy to include other cell types, such as ventral mesendodermal cells (Please see Author response image 2A). Based on this, we believe that directly using embryonic data to decipher the mechanism of fate differentiation between the PP and the anterior endoderm may not yield sufficiently precise results. In contrast, our group’s previous study published in Cell Reports demonstrated that the Nodal-induced explant system can specifically enrich dorsal mesendodermal cells, including the anterior endoderm, PP, and notochord[5]. Thus, we consider the Nodal explant system as an ideal model for studying the fate differentiation mechanism between the PP and the anterior endoderm. Ultimately, through comprehensive analysis of in vivo embryonic data and Nodal explant data, we consistently found that the anterior endoderm likely originates from PP progenitor cells—a conclusion further validated by live imaging experiments.

Regarding the GO analysis, we have streamlined it as suggested by the reviewers. In the revised manuscript, we analyzed the expression of specific genes contributing to key GO functions. Additionally, in the revised version, we conducted more live imaging experiments and quantitative cell assays. We designed gRNA for srcap using the CRISPR CAS13 system to knock down srcap, which further corroborated the morpholino knockdown results, showing consistency with the morpholino data. We also performed Western blot validation of the SWI/SNF complex's response to the drug AU15330, confirming the drug's effectiveness. We hope these additional experiments adequately address the reviewers' concerns.

Reviewer #2 (Recommendations For The Authors):

(1) In the introduction, the authors state that mesendoderm segregates into mesoderm and endoderm in a Nodal-concentration dependent manner. While it is true that higher Nodal signaling levels are required for endoderm specification, A) this is also true for some mesoderm populations, and B) Work from Caroline Hill's lab has shown that Nodal activity alone is not determinative of endoderm fate. Although the authors cite this work, it is conclusions are not reflected in this over-simplified explanation of mesendoderm development. The authors also state that it is not clear when PP and endoderm can be distinguished transcriptionally, but this was also addressed in Economou et al, 2022, which found that they can be distinguished at 60% epiboly but not 50% epiboly.

We sincerely thank the reviewer for raising this question and reminding us of the conclusions drawn from that excellent study. As the reviewer pointed out, Economou et al. demonstrated that Nodal signaling alone is insufficient to determine the cell fate segregation of mesendoderm[6]. However, their study primarily focused on the fate segregation of the ventral-lateral mesendoderm lineage. In contrast, we believe that the mechanisms underlying dorsal mesendoderm specification may differ.

First, it is well-studied that in zebrafish embryos, the most dorsal mesendoderm is initially specified by the activity of the dorsal organizer. Notably, the Nodal signaling ligands ndr1 and ndr2 begin to be expressed in the dorsal organizer as early as the sphere stage[7]. In our study, through single-cell transcriptomic trajectory analysis and live imaging analysis, we observed that the cell fate segregation of the dorsal mesendoderm can be traced back to the shield stage.

Second, the regulatory mechanisms governing dorsal mesendoderm fate differentiation may differ from those of the ventral-lateral mesendoderm. For instance, the gsc gene is exclusively expressed in the dorsal mesendoderm and is absent in the ventral-lateral mesendoderm. Given that gsc is a critical master gene, its overexpression in the ventral side can induce a complete secondary body axis. Similarly, ripply1, identified in our study, is also expressed early and specifically in the dorsal mesendoderm. Overexpression of ripply1 in the ventral side similarly induces a secondary body axis, albeit with the absence of the forebrain[5]. In this study, we found that gsc and ripply1 as the repressor, collectively inhibited dorsal (anterior) endoderm specified from PP progenitors.

In summary, our study focuses on the regulatory mechanisms of fate segregation in the dorsal (anterior) mesendoderm, which differs from the mechanisms of ventral-lateral mesendoderm lineage segregation reported by Economou et al. We believe that this distinction represents a key novelty of our work.

(2) As noted in the manuscript, Warga and Nusslein-Volhard determined long ago that PP and anterior endoderm share a common precursor. It is surprising that this close relationship is not apparent from the lineage trees in whole embryos but is apparent in lineage trees from explants. The authors speculate that the resolution of the whole embryo dataset is insufficient to detect this branch point and propose explants as the solution, but it is not clear why the explant dataset is higher resolution and/or more appropriate to address this question.

We sincerely thank the reviewer for their thoughtful comments. As we mentioned previously, our investigation of fate differentiation between the PP and the anterior endoderm initially involved the analysis of zebrafish embryonic data. However, when we used URD to reconstruct the transcriptional trajectory tree, we observed that these two cell trajectories were located far apart. Previous elegant studies, as the reviewer mentioned, have shown that the anterior endoderm and the PP are not only spatially adjacent but also both originate from mesendodermal progenitor cells and share transcriptional similarities[2,3,8]. Consequently, when tracing all progenitor cells of these two trajectories using the URD algorithm, other cell types—such as ventral mesendodermal cells—are easily included. Based on this, we believe that directly using embryonic data to elucidate the mechanism of fate differentiation between the PP and the anterior endoderm may lack sufficient precision.

In contrast, our group’s previous study published in Cell Reports demonstrated that the Nodal-induced explant system specifically enriches dorsal mesendodermal cells, including the anterior endoderm, PP, and notochord[5]. Therefore, we consider the Nodal explant system as an ideal model for studying the mechanism underlying fate differentiation between the PP and the anterior endoderm. Through comprehensive analyses of both in vivo embryonic and Nodal explant data, we consistently found that the anterior endoderm likely originates from PP progenitor cells—a conclusion further supported by live imaging experiments.

(3) Much of the analysis of DEGs between the lineages of interest is focused on GO term enrichment. But this logic is circular. The endoderm lineage is defined as such because it expresses endoderm-enriched genes, therefore the finding that the endoderm lineage is enriched for endoderm-related GO terms adds no new insights.

We thank the reviewer for these comments. As the reviewers suggested, in the revised manuscript, we indicated specific genes associated with key GO terms (Please see Figure 4B). Additionally, we have streamlined the content related to the GO analysis as suggested.

(4) The authors describe the experiment in Figure S4 as key evidence that Gsc+ cells can give rise to endoderm, but no controls are presented. Only a few cells are shown that express mCherry upon injection of sox17:cre constructs. Is mCherry also expressed in the occasional cell injected with Gsc:lox-stop-lox-mCherry in the absence of cre? Although they report 3 independent replicates, it appears that only 2 individual embryos express mCherry. This very small number is not convincing, especially in the absence of appropriate controls.

We thank the reviewer for raising this question. Following the reviewer's suggestion, we injected gsc:loxp-stop-loxp-mCherry into zebrafish embryos at the 1-cell stage as a control. After performing at least three independent replicates and analyzing no fewer than 100 embryos, we did not observe any mCherry-positive cells. Additionally, we co-injected gsc:loxp-stop-loxp-mCherry with sox17:cre and increased the sample size. Furthermore, we constructed plasmids of sox17:loxp-stop-loxp-mCherry and gsc:cre, and upon injection at the 1-cell stage, we observed RFP-positive cells at 8 hpf (Please see Author response image 1 and Figure S4E). Together with our live imaging data, these experiments collectively demonstrate that anterior endodermal cells can originate from PP progenitors.

(5) The authors spend a lot of effort demonstrating that PP and anterior endoderm are Nodal dependent. First, these data (especially Figures 3E and 3I) are not very convincing, as the differences shown are very small or not apparent. Second, this is already well-known and adds nothing to our understanding of mesoderm-endoderm segregation.

We sincerely thank the reviewer for their insightful questions. First, the reviewer mentioned that in the initial version of our manuscript, the effects of ndr1 knockdown and lefty1 knockout on Nodal signaling and cell fate—particularly prechordal plate (PP) and anterior endoderm (endo)—in Nodal-induced explants were not very pronounced. We recognize that the negative feedback mechanism between Nodal and Lefty signaling may explain why Nodal acts as a morphogen, regulating pattern formation through a Turing-like model[9]. Therefore, knocking down a Nodal ligand gene, such as ndr1 in this study, or knocking out a Nodal inhibitor, such as lft1, may only have a subtle impact on Nodal signaling[10].

Accordingly, in this study, we performed extensive pSmad2 immunofluorescence analysis and observed that although the overall intensity of Nodal activity did not change dramatically, there was a statistically significant difference. Importantly, this subtle variation in Nodal signaling strength is precisely what we intended to capture, since PP and anterior endoderm are highly sensitive to Nodal signaling[11], and even minor differences may bias their fate segregation.

This leads directly to the reviewer’s second concern. While numerous studies suggest that the strength of Nodal signaling influences mesendodermal fate—with high Nodal promoting endoderm and lower concentrations inducing mesoderm—most of these studies focus on ventral-lateral mesendoderm development[4,6,10]. In contrast, the mechanisms underlying dorsal mesendoderm fate specification differ, which is a key innovation of our study.

Previous work by Bernard Thisse and colleagues demonstrated that even a slight reduction in Nodal signaling, achieved by overexpressing a Nodal inhibitor, is sufficient to cause defects in the specification of PP and endoderm[11]. This indicates that PP and endoderm require the highest levels of Nodal signaling for proper specification. Moreover, the most dorsal mesendoderm, PP and anterior endoderm are not only spatially adjacent but also share similar transcriptional states, making the regulation of their fate separation particularly challenging to study.

The Dr. C.P. lab made important contributions to this issue, showing that the duration of Nodal exposure is critical for segregating PP and anterior endoderm fates: prolonged Nodal signaling promotes expression of the transcriptional repressor Gsc, which directly suppresses the key endodermal transcription factor Sox17, thereby inhibiting anterior endoderm specification[3]. They also found that tight junctions among PP cells facilitate Nodal signal propagation[8]. However, their studies revealed that Gsc mutants do not exhibit endodermal phenotypes, suggesting that additional factors or mechanisms regulate PP versus anterior endoderm fate separation[3].

In our study, we first observed that subtle differences in Nodal concentration may bias the fate choice between PP and anterior endoderm. Given that ndr1 knockdown and lft1 knockout mildly reduce or enhance Nodal signaling, respectively, we reasoned that using these two perturbations in a Nodal-induced explant system combined with single-cell RNA sequencing could generate transcriptomic profiles under slightly reduced and enhanced Nodal signaling. This approach may help identify key decision points and transcriptional differences during PP and anterior endoderm segregation, ultimately uncovering the molecular mechanisms downstream of Nodal that govern their fate separation.

(6) The authors claim that scrap expression differs between the 2 lineages of interest, but this is not apparent from Figure 4J-K. Experiments testing the role of SWI/SNF and scrap also require additional controls. Can scrap MO phenotypes be rescued by scrap RNA? Is there validation that SWI/SNF components are degraded upon treatment with AU15330?

We are very grateful for the reviewers' questions. Using single-cell data from zebrafish embryos and Nodal explants, we compared the expression of srcap in the PP and anterior Endo cell populations. We found that srcap expression showed a slight increase in PP compared to anterior Endo, but the difference was not statistically significant (Please see Figure 4J and S7H). Therefore, we modified our description in the revised manuscript. However, we speculate that this slight difference might influence the distinct cell fate specification between PP and anterior endo. In the original version of the manuscript, we reported that either treatment with AU15330, an inhibitor of the SWI/SNF complex, or injection of morpholino targeting srcap—a key component of the SWI/SNF complex—enhanced anterior endo fate while reducing PP cell specification. During this round of revision, we initially attempted to follow the reviewer’s suggestion to co-inject srcap mRNA along with srcap morpholino to rescue the phenotype. However, we found that the length of srcap mRNA exceeds 10,000 bp, and despite multiple attempts, we were unable to successfully obtain the srcap mRNA. Therefore, we were unable to perform the rescue experiment and instead adopted an alternative approach to validate the function of srcap. We aimed to use anthor knockdown approach (CRISPR/Cas system) to determine whether a phenotype similar to that observed with morpholino knockdown could be achieved. Using the CRISPR/Cas13 system, we designed gRNA targeting srcap, knocked down srcap, and examined the cell specification of PP and anterior endo. We found that, consistent with our previous results, knocking down srcap obviously reduced PP cell fate while increasing anterior endo cell fate (Author response image 3). Additionally, the reviewer raised the question of whether the SWI/SNF complex is degraded after AU15330 treatment. Following the reviewer’s suggestion, we attempted to perform Western blot analysis on BRG1, one of the components of the SWI/SNF complex. However, despite multiple attempts, we were unable to achieve successful detection of the BRG1 protein by the antibody in zebrafish. Several studies have reported that knockdown or knockout of brg1 leads to defects in neural crest cell specification in zebrafish[12,13]. Therefore, alternatively, we treated zebrafish embryos at the one-cell stage with 0 μM (DMSO), 1 μM, and 5 μM AU15330, and examined the expression of sox10 and pigment development around 48 h. We found that treatment with 1 μM AU15330 reduced sox10 expression and pigment production, though not significantly, whereas treatment with 5 μM AU15330 significantly disrupted neural crest cell development. Thus, this experiment demonstrates that AU15330 is functional in zebrafish. (Author response image 3).

Author response image 3.

(A) Characterization of anterior endoderm and PP cells following CRISPR-Cas13d-mediated srcap knockdown. (B) Validation of srcap mRNA expression by RT‑qPCR following CRISPR‑Cas13d knockdown. (C) RT‑qPCR shows the expression of sox10 after treatment with increasing concentrations of AU15300. (D) Morphology of zebrafish embryos at 48 hpf after treatment with increasing concentrations of AU15300.

(7) The authors conclude from their chromatin accessibility analysis that variations in Nodal signaling are responsible for expression levels of PP and endoderm genes, but they do not consider the alternative explanation that FGF signaling is playing this role. Such a function for FGF was established by Caroline Hill's lab, and the authors also show in Figure S5G that FGF signaling in enriched between these cell populations.

Thank you very much for raising this issue. As the reviewer pointed out, Caroline Hill's lab has conducted elegant work demonstrating that FGF signaling plays a crucial role in the separation of ventral-lateral mesendoderm cell fates[4,6]. In contrast, our study primarily focuses on studying the mechanisms underlying the separation of dorsal mesendoderm cell fates. However, our research also reveals that FGF signaling significantly regulates the fate separation of the dorsal mesendoderm, as inhibiting FGF signaling suppresses PP cell specification while promoting anterior Endo fate. In our previously published work, we found that Nodal signaling can directly activate the expression of FGF ligand genes[5]. Therefore, we hypothesize that Nodal signaling, acting as a master regulator, activates various downstream target genes—including FGF—and how FGF signaling regulates the cell fate separation of the dorsal mesendoderm warrants further investigation in our further studies.

(8) When interpreting the results of their Ripply cut-and-run experiment, the authors again rely heavily on GO term analysis and claim that this supports a role for Ripply as a transcriptional repressor. GO term enrichment does not equal functional analysis. It would be more convincing to intersect DEGs between WT and ripply-/- embryos with Ripply-enriched loci.

Thanks for raising this important issue and the constructive suggestion. In response to the reviewer's valid concern regarding the GO term analyses from our CUT&Tag data, we implemented a more stringent filtering strategy. We identified peaks enriched in the treatment group and applied differential analysis, selecting genes with a log₂FoldChange > 3, padj < 0.05, and baseMean > 30 as high-confidence Ripply1 binding targets. A GO enrichment analysis of these genes revealed significant terms related to muscle development, consistent with Ripply1's established role in somite development, thereby validating our approach. We supplemented the related gene list in the revised manuscript. Moreover, within this refined analysis, we found that sox32 met our binding threshold, while sox17 did not. Furthermore, as suggested, we examined mespbb—a known Ripply1-repressed gene—which was present, and gsc, a Nodal target used as a negative control, which was absent. This confirms the specificity of our analysis (Figure 6 and Figure S11). Consequently, our revised analyses support a model in which Ripply1 directly binds the sox32 promoter. Given that Sox32 is a known upstream regulator of sox17, this binding provides a plausible direct mechanism for the observed regulation of sox17 expression. We have updated the figures and text accordingly. We attempted to generate ripply1^-/- mutants but found that homozygous loss results in embryonic lethality.

(9) The way N's are reported is unconventional. N= number of embryos used in the experiment, n= number of embryos imaged. If an embryo was not imaged or analyzed in any way, it cannot be considered among the embryos in an experiment. If only 4 embryos were imaged, the N for that experiment is 4 regardless of how many embryos were stained. Authors should also report not only the number of embryos examined but also the number of independent trials performed for all experiments.

Thank you very much for the reviewer's suggestion. As suggested, we have revised the description regarding the number of embryos and experimental replicates in the figure legends.

(10) The authors should avoid the use of red-green color schemes in figures to ensure accessibility for color-blind readers.

Thanks for the suggestions. We have updated the figures in our revised manuscript and adjusted the color schemes to avoid red-green combinations.

Reviewer #3 (Public Review):

Summary:

Cheng, Liu, Dong, et al. demonstrate that anterior endoderm cells can arise from prechordal plate progenitors, which is suggested by pseudo time reanalysis of published scRNAseq data, pseudo time analysis of new scRNAseq data generated from Nodal-stimulated explants, live imaging from sox17:DsRed and Gsc:eGFP transgenics, fluorescent in situ hybridization, and a Cre/Lox system. Early fate mapping studies already suggested that progenitors at the dorsal margin give rise to both of these cell types (Warga) and live imaging from the Heisenberg lab (Sako 2016, Barone 2017) also pretty convincingly showed this. However, the data presented for this point are very nice, and the additional experiments in this manuscript, however, further cement this result. Though better demonstrated by previous work (Alexander 1999, Gritsman 1999, Gritsman 2000, Sako 2016, Rogers 2017, others), the manuscript suggests that high Nodal signaling is required for both cell types, and shows preliminary data that suggests that FGF signaling may also be important in their segregation. The manuscript also presents new single-cell RNAseq data from Nodal-stimulated explants with increased (lft1 KO) or decreased (ndr1 KD) Nodal signaling and multi-omic ATAC+scRNAseq data from wild-type 6 hpf embryos but draws relatively few conclusions from these data. Lastly, the manuscript presents data that SWI/SNF remodelers and Ripply1 may be involved in the anterior endoderm - prechordal plate decision, but these data are less convincing. The SWI/SNF remodeler experiments are unconvincing because the demonstration that these factors are differentially expressed or active between the two cell types is weak. The Ripply1 gain-of-function experiments are unconvincing because they are based on incredibly high overexpression of ripply1 (500 pg or 1000 pg) that generates a phenotype that is not in line with previously demonstrated overexpression studies (with phenotypes from 10-20x lower expression). Similarly, the cut-and-tag data seems low quality and like it doesn't support direct binding of ripply1 to these loci.

In the end, this study provides new details that are likely important in the cell fate decision between the prechordal plate and anterior endoderm; however, it is unclear how Nodal signaling, FGF signaling, and elements of the gene regulatory network (including Gsc, possibly ripply1, and other factors) interact to make the decision. I suggest that this manuscript is of most interest to Nodal signaling or zebrafish germ layer patterning afficionados. While it provides new datasets and observations, it does not weave these into a convincing story to provide a major advance in our understanding of the specification of these cell types.

We sincerely thank the reviewer for their thorough and thoughtful assessment of our work. The reviewer acknowledged several strengths of our study, such as the use of multiple technical approaches to demonstrate that anterior endoderm differentiates from PP progenitor cells, and recognized the value of the newly added single-cell omics data. The reviewer also raised some concerns regarding the initial version of our work, including the SWI/SNF remodeler experiments and the Ripply1 gain-of-function experiment. In the revised manuscript, we have supplemented these parts with additional control experiments to better support our conclusions. We hope that our updated manuscript adequately addresses the points raised by the reviewer.

Major issues:

(1) UMAPs: There are several instances in the manuscript where UMAPs are used incorrectly as support for statements about how transcriptionally similar two populations are. UMAP is a stochastic, non-linear projection for visualization - distances in UMAP cannot be used to determine how transcriptionally similar or dissimilar two groups are. In order to make conclusions about how transcriptionally similar two populations are requires performing calculations either in the gene expression space, or in a linear dimensional reduction space (e.g. PCA, keeping in mind that this will only consider the subset of genes used as input into the PCA). Please correct or remove these instances, which include (but are not limited to):

p.4 107-110

p.4 112

p.8 207-208

p.10 273-275

We would like to thank the reviewer for raising this question. The descriptions of UMAP have been revised throughout the manuscript in accordance with the reviewer's suggestion (Please see the main text in the revised manuscript).

(2) Nodal and lefty manipulations: The section "Nodal-Lefty regulatory loop is needed for PP and anterior Endo fate specification" and Figure 3 do not draw any significant conclusions. This section presents a LIANA analysis to determine the signals that might be important between prechordal plate and endoderm, but despite the fact that it suggests that BMP, Nodal, FGF, and Wnt signaling might be important, the manuscript just concludes that Nodal signaling is important. Perhaps this is because the conclusion that Nodal signaling is required for the specification of these cell types has been demonstrated in zebrafish in several other studies with more convincing experiments (Alexander 1999, Gritsman 1999, Gritsman 2000, Rogers 2017, Sako 2016). While FGF has recently been demonstrated to be a key player in the stochastic decision to adopt endodermal fate in lateral endoderm (Economou 2022), the idea that FGF signaling may be a key player in the differentiation of these two cell types has strangely been relegated to the discussion and supplement. Lastly, the manuscript does not make clear the advantage of performing experiments to explore the PP-Endo decision in Nodal-stimulated explants compared to data from intact embryos. What would be learned from this and not from an embryo? Since Nodal signaling stimulates the expression of Wnts and FGFs, these data do not test Nodal signaling independent of the other pathways. It is unclear why this artificial system that has some disadvantages is used since the manuscript does not make clear any advantages that it might have had.

We sincerely thank the reviewers for their valuable comments. As mentioned in our manuscript, although a substantial number of studies have reported on the mechanisms governing the segregation of mesendoderm fate in zebrafish embryos—including the Dr. Hill laboratory’s work cited by the reviewers, which demonstrated the involvement of FGF signaling in the ventral mesendoderm fate specification—research on the regulatory mechanisms underlying anterior mesendoderm differentiation remains relatively limited. This is largely due to the challenges posed by the close physical proximity and similar transcriptional states of anterior mesendoderm cells, as well as their shared dependence on high levels of Nodal signaling for specification.

Several studies from the Dr. C.P. Heisenberg’s laboratory have attempted to elucidate the fate segregation between anterior mesendoderm cells, namely the prechordal plate (PP) and anterior endoderm (endo) cells. They found that PP cells are tightly connected, facilitating the propagation of Nodal signaling[8]. Prolonged exposure to Nodal activates the expression of Gsc, which acts as a transcriptional repressor to inhibit sox17 expression, thereby suppressing endodermal fate[3]. However, they also noted that Gsc mutants do not exhibit endoderm developmental defects, suggesting the involvement of additional factors in this process.

The reviewer inquired about our rationale for using the Nodal-injected explant system. In our investigation of the fate separation between the PP and the anterior endo, we initially analyzed zebrafish embryonic data. Using URD to reconstruct the transcriptional lineage tree, we found that these two cell types were positioned distantly from each other. However, existing literature indicates that the anterior endoderm and PP are not only spatially adjacent but also derive from common mesendodermal progenitors and exhibit transcriptional similarities[2,8]. As the reviewer noted, when tracing all progenitor cells of these two lineages using URD, it is easy to inadvertently include other cell types—such as ventral epiblast cells—which may compromise the accuracy of the analysis. We therefore concluded that directly using embryonic data to dissect the mechanism of fate separation between PP and anterior endoderm might not yield highly precise results.

By contrast, our group’s earlier study published in Cell Reports demonstrated that the Nodal-induced explant system specifically enriches dorsal mesendodermal cells, including anterior endo, PP, and notochord[5]. This makes the Nodal explant system a highly suitable model for studying the fate separation between PP and anterior endo. Ultimately, by analysing in vivo embryonic data and Nodal explant data, we consistently found that the anterior endoderm likely originates from PP progenitors—a conclusion further supported by live imaging experiments.

As we answered above, we first used the analyses of single-cell RNA sequencing and live imaging to demonstrate that anterior endoderm can originate from PP progenitor cells. Understanding the mechanism underlying the fate segregation between these two cell populations became a key focus of our research. We began by applying cell communication analysis to our single-cell data to identify signaling pathways that may be involved. This analysis specifically highlighted the Nodal-Lefty signaling pathway. Since Lefty acts as an inhibitor of Nodal signaling, we hypothesized that differences in Nodal signaling strength might regulate the fate of these two cell populations. By overexpressing different concentrations of Nodal mRNA and examining the fates of PP and anterior Endo cells, we confirmed this hypothesis.

Thus, we propose that even subtle differences in Nodal signaling levels may influence anterior mesendoderm fate decisions. To test this, we generated systems with slightly reduced Nodal signaling (via ndr1 knockdown) and slightly elevated Nodal signaling (via lft1 knockout). Using these models, we precisely captured the critical stage of fate segregation between PP and anterior endo cells and identified a novel transcriptional repressor, Ripply1, which works in concert with Gsc to suppress anterior endoderm differentiation.

(3) ripply1 mRNA injection phenotype inconsistent with previous literature: The phenotype presented in this manuscript from overexpressing ripply1 mRNA (Fig S11) is inconsistent with previous observations. This study shows a much more dramatic phenotype, suggesting that the overexpression may be to a non-physiological level that makes it difficult to interpret the gain-of-function experiments. For instance, Kawamura et al 2005 perform this experiment but do not trigger loss of head and eye structures or loss of tail structures. Similarly, Kawamura et al 2008 repeat the experiment, triggering a mildly more dramatic shortening of the tail and complete removal of the notochord, but again no disturbance of head structures as displayed here. These previous studies injected 25 - 100 pg of ripply1 mRNA with dramatic phenotypes, whereas this study uses 500 - 1000 pg. The phenotype is so much more dramatic than previously presented that it suggests that the level of ripply1 overexpression is sufficiently high that it may no longer be regulating only its endogenous targets, making the results drawn from ripply1 overexpression difficult to trust.

We sincerely thank the reviewer for raising this question. First, we apologize for not providing a detailed description of the amount of HA-ripply1 mRNA injected in our previous manuscript. We injected 500 pg of HA-ripply1 mRNA at the 1-cell stage and allowed the embryos to develop until 6 hpf for the CUT&Tag experiment. In the supplementary materials, we included a bright-field image of an 18 hpf-embryo injected with HA-ripply1 mRNA, which morphologically exhibited severe developmental abnormalities. The reviewer pointed out that the amount of ripply1 mRNA we injected might be excessive, potentially leading to non-specific gain-of-function effects. The injection dose of 500 pg was determined based on conclusions from our previous study. In that study, injecting 24 pg of ripply1 mRNA into one cell of zebrafish embryos at the 16–32 cell stage was sufficient to induce a secondary axis lacking the forebrain[5]. From this, we estimated that an injection concentration of approximately 500–1000 pg would be appropriate at the 1-cell stage, so that after several rounds of cell division, each cell gained 20-30 pg mRNA at 32 cell stage. Additionally, we conducted supplementary experiments injecting 100 pg, 250 pg, and 500 pg of ripply1 mRNA, and observed 500 pg of ripply1 mRNA led to a dramatic suppression of endoderm formation (Author response image 4).

Finally, our study focuses on the mechanism of cell fate segregation in the anterior mesendoderm, primarily during gastrulation. The embryos injected with ripply1 mRNA underwent normal gastrulation, and our CUT&Tag experiment was performed at 6 hpf. Therefore, we believe that the amount of ripply1 mRNA injected in this study is appropriate for addressing our research question.

Author response image 4.

Different concentrations of ripply1 mRNA were injected into zebrafish embryos at the one-cell stage, with RFP fluorescence labeling sox17-positive cells.

(4) Ripply1 binding to sox17 and sox32 regulatory regions not convincing: The Cut and Tag data presented in Fig 6J-K does not seem to be high quality and does not seem to provide strong support that Ripply 1 binds to the regulatory regions of these genes. The signal-to-noise ratio is very poor, and the 'binding' near sox17 that is identified seems to be even coverage over a 14 kb region, which is not consistent with site-specific recruitment of this factor, and the 'peaks' highlighted with yellow boxes do not appear to be peaks at all. To me, it seems this probably represents either: (1) overtagmentation of these samples or (2) an overexpression artifact from injection of too high concentration of ripply1-HA mRNA. In general, Cut and Tag is only recommended for histone modifications, and Cut and Run would be recommended for transcriptional regulators like these (see Epicypher's literature). Given this and the previous point about Ripply1 overexpression, I am not convinced that Ripply1 regulates endodermal genes. The existing data could be made somewhat more convincing by showing the tracks for other genes as positive and negative controls, given that Ripply1 has known muscle targets (how does its binding look at those targets in comparison) and there should be a number of Nodal target genes that Ripply1 does not bind to that could be used as negative controls. Overall this experiment doesn't seem to be of high enough quality to drive the conclusion that Ripply1 directly binds near sox17 and sox32 and from the data presented in the manuscript looks as if it failed technically.

We sincerely thank the reviewer for raising this question. We apologize that the binding regions of sox17 marked in our previous analysis were incorrect, and we have made the corresponding revisions in the latest version of the manuscript.

The reviewer noted that our CUT&Tag data contain considerable noise. To address this, we further refined our data processing: we annotated all peaks enriched in the treatment group and performed differential analysis, selecting genes with log₂FoldChange > 3, padj < 0.5, and baseMean > 30 as candidate targets of Ripply1 binding. Subsequent GO enrichment analysis of these genes revealed significant enrichment of muscle development-related GO terms, which is consistent with previously reported roles of Ripply1 in regulating somite development. Therefore, we believe our filtering method effectively removes a large number of noise peaks and their associated genes.

Under these screening criteria, we found that sox32 meets the threshold, while sox17 does not. In addition, following the reviewer’s suggestion, we examined mespbb—a known gene repressed by Ripply1—and gsc, a Nodal target gene, as a negative control.

Based on these new analyses, we have revised our figures and text accordingly. Our data now support the possibility that Ripply1 may directly bind to the promoter region of sox32. Since sox32 acts as a direct upstream regulator of sox17, this binding could influence sox17 expression (Figure 6 and Figure S11).

Finally, we would like to note that studies have reported Ripply1 as a transcriptional repressor, which may function by recruiting other co-factors, such as Groucho, to form a complex[14,15]. This might explain why our CUT&Tag data detected Ripply1 binding to a broad set of genes.

(5) "Cooperatively Gsc and ripply1 regulate": I suggest avoiding the term "cooperative," when describing the relationship between Ripply1 and Gsc regulation of PP and anterior endoderm - it evokes the concept of cooperative gene regulation, which implies that these factors interact with each biochemically in order to bind to the DNA. This is not supported by the data in this manuscript, and is especially confusing since Ripply1 is thought to require cooperative binding with a T-box family transcription factor to direct its binding to the DNA.

We sincerely thank the reviewer for raising this important issue. The reviewer pointed out that the term "Cooperatively" may not be entirely appropriate in the context of our study. In accordance with the reviewer's suggestion, we have replaced "Cooperatively" with "Collectively" in the relevant sections.

(6) SWI/SNF: The differential expression of srcap doesn't seem very remarkable. The dot plots in the supplement S7H don't help - they seem to show no expression at all in the endoderm, which is clearly a distortion of the data, since from the violin plots it's obviously expressed and the dot-size scale only ranges from ~30-38%. Please add to the figure information about fold-change and p-value for the differential expression. Publicly available scRNAseq databases show scrap is expressed throughout the entire early embryo, suggesting that it would be surprising for it to have differential activity in these two cell types and thereby contribute to their separate specification during development. It seems equally possible that this just mildly influences the level of Nodal or FGF signaling, which would create this effect.

Thank the Reviewer for this question. As suggested, we performed Wilcoxon tests to compare srcap expression between PP and Endo populations. The analysis shows that while srcap expression is moderately elevated in PP compared to in Endo, this difference is not statistically significant. The corresponding p-value and fold change have now been included in the revised figure (Please see Figure 4J and S7H). Although the transcriptional level of srcap shows no significant difference between PP and anterior endoderm, our subsequent experiments—using AU15330 (an inhibitor of the SWI/SNF complex) and injecting morpholino targeting srcap, a key component of the SWI/SNF complex—demonstrated that its inhibition indeed promotes anterior endoderm fate while reducing PP cell specification. Therefore, we propose that subtle differences in the SWI/SNF complex may regulate the fate specification of PP and anterior endoderm through two mechanisms. First, as mentioned in our study, these chromatin remodelers modulate the expression of master regulators such as Gsc and Ripply1, thereby influencing cell fate decisions. Second, as noted by the reviewer, these chromatin remodelers may affect the interpretation of Nodal signaling, ultimately contributing to the divergence between PP and anterior endoderm fates.

The multiome data seems like a valuable data set for researchers interested in this stage of zebrafish development. However, the presentation of the data doesn't make many conclusions, aside from identifying an element adjacent to ripply1 whose chromatin is open in prechordal plate cells and not endodermal cells and showing that there are a number of loci with differential accessibility between these cell types. That seems fairly expected since both cell types have several differentially expressed transcriptional regulators (for instance, ripply1 has previously been demonstrated in multiple studies to be specific to the prechordal plate during blastula stages). The manuscript implies that SWI/SNF remodeling by Srcap is responsible for the chromatin accessibility differences between these cell types, but that has not actually been tested. It seems more likely that the differences in chromatin accessibility observed are a result of transcription factors binding downstream of Nodal signaling.

We thank the reviewer for recognizing the value of our newly generated data. Through integrative analysis of single-cell data from wild-type, ndr1 kd, and lft1 ko groups of Nodal-injected explants at 6 hours post-fertilization (hpf), we identified a critical branching point in the fate segregation of the prechordal plate (PP) and anterior endoderm (Endo), where chromatin remodelers may play a significant role. Based on this finding, we performed single-cell RNA and ATAC sequencing on zebrafish embryos at 6 hpf. Analysis of this multi-omics dataset revealed that transcriptional repressors such as Gsc, Ripply1, and Osr1 exhibit differences in both transcriptional and chromatin accessibility levels between the PP and anterior Endo. Subsequent overexpression and loss-of-function experiments further demonstrated that Gsc and Ripply1 collaboratively suppress endodermal gene expression, thereby inhibiting endodermal cell fate. Previous studies have reported that for the activation of certain Nodal downstream target genes, the pSMAD2 protein of the Nodal signaling pathway recruits chromatin remodelers to facilitate chromatin opening and promote further transcription of target genes[16]. Therefore, our data provide chromatin accessibility profiles for Gsc and Ripply1, offering a valuable resource for future investigations into their pSMAD2 binding sites.

Minor issues:

Figure 2 E-F: It's not clear which cells from E are quantitated in F. For instance, the dorsal forerunner cells are likely to behave very differently from other endodermal progenitors in this assay. It would be helpful to indicate which cells are analyzed in Fig F with an outline or other indicator of some kind. Or - if both DFCs and endodermal cells are included in F, to perhaps use different colors for their points to help indicate if their fluorescence changes differently.

Thank you for the reviewer's suggestion. In the revised version of the figure, we have outlined the regions of the analyzed cells.

Fig 3 J: Should the reference be Dubrulle et al 2015, rather than Julien et al?

Thanks, we have corrected.

References:

Alexander, J. & Stainier, D. Y. A molecular pathway leading to endoderm formation in zebrafish. Current biology : CB 9, 1147-1157 (1999).

Barone, V. et al. An Effective Feedback Loop between Cell-Cell Contact Duration and Morphogen Signaling Determines Cell Fate. Dev. Cell 43, 198-211.e12 (2017).

Economou, A. D., Guglielmi, L., East, P. & Hill, C. S. Nodal signaling establishes a competency window for stochastic cell fate switching. Dev. Cell 57, 2604-2622.e5 (2022).

Gritsman, K. et al. The EGF-CFC protein one-eyed pinhead is essential for nodal signaling. Cell 97, 121-132 (1999).

Gritsman, K., Talbot, W. S. & Schier, A. F. Nodal signaling patterns the organizer. Development (Cambridge, England) 127, 921-932 (2000).

Kawamura, A. et al. Groucho-associated transcriptional repressor ripply1 is required for proper transition from the presomitic mesoderm to somites. Developmental cell 9, 735-744 (2005).

Kawamura, A., Koshida, S. & Takada, S. Activator-to-repressor conversion of T-box transcription factors by the Ripply family of Groucho/TLE-associated mediators. Molecular and cellular biology 28, 3236-3244 (2008).

Sako, K. et al. Optogenetic Control of Nodal Signaling Reveals a Temporal Pattern of Nodal Signaling Regulating Cell Fate Specification during Gastrulation. Cell Rep. 16, 866-877 (2016).

Rogers, K. W. et al. Nodal patterning without Lefty inhibitory feedback is functional but fragile. eLife 6, e28785 (2017).

Warga, R. M. & Nüsslein-Volhard, C. Origin and development of the zebrafish endoderm. Development 126, 827-838 (1999).

References:

(1) Steinbeisser, H., and De Robertis, E.M. (1993). Xenopus goosecoid: a gene expressed in the prechordal plate that has dorsalizing activity. C R Acad Sci III 316, 959-971.

(2) Warga, R.M., and Nusslein-Volhard, C. (1999). Origin and development of the zebrafish endoderm. Development (Cambridge, England) 126, 827-838. 10.1242/dev.126.4.827.

(3) Sako, K., Pradhan, S.J., Barone, V., Inglés-Prieto, Á., Müller, P., Ruprecht, V., Čapek, D., Galande, S., Janovjak, H., and Heisenberg, C.P. (2016). Optogenetic Control of Nodal Signaling Reveals a Temporal Pattern of Nodal Signaling Regulating Cell Fate Specification during Gastrulation. Cell reports 16, 866-877. 10.1016/j.celrep.2016.06.036.

(4) van Boxtel, A.L., Economou, A.D., Heliot, C., and Hill, C.S. (2018). Long-Range Signaling Activation and Local Inhibition Separate the Mesoderm and Endoderm Lineages. Developmental cell 44, 179-191.e175. 10.1016/j.devcel.2017.11.021.

(5) Cheng, T., Xing, Y.Y., Liu, C., Li, Y.F., Huang, Y., Liu, X., Zhang, Y.J., Zhao, G.Q., Dong, Y., Fu, X.X., et al. (2023). Nodal coordinates the anterior-posterior patterning of germ layers and induces head formation in zebrafish explants. Cell reports 42, 112351. 10.1016/j.celrep.2023.112351.

(6) Economou, A.D., Guglielmi, L., East, P., and Hill, C.S. (2022). Nodal signaling establishes a competency window for stochastic cell fate switching. Developmental cell 57, 2604-2622 e2605. 10.1016/j.devcel.2022.11.008.

(7) Schier, A.F., and Talbot, W.S. (2005). Molecular genetics of axis formation in zebrafish. Annual review of genetics 39, 561-613. 10.1146/annurev.genet.37.110801.143752.

(8) Barone, V., Lang, M., Krens, S.F.G., Pradhan, S.J., Shamipour, S., Sako, K., Sikora, M., Guet, C.C., and Heisenberg, C.P. (2017). An Effective Feedback Loop between Cell-Cell Contact Duration and Morphogen Signaling Determines Cell Fate. Developmental cell 43, 198-211.e112. 10.1016/j.devcel.2017.09.014.

(9) Muller, P., Rogers, K.W., Jordan, B.M., Lee, J.S., Robson, D., Ramanathan, S., and Schier, A.F. (2012). Differential diffusivity of Nodal and Lefty underlies a reaction-diffusion patterning system. Science (New York, N.Y.) 336, 721-724. 10.1126/science.1221920.

(10) Rogers, K.W., Lord, N.D., Gagnon, J.A., Pauli, A., Zimmerman, S., Aksel, D.C., Reyon, D., Tsai, S.Q., Joung, J.K., and Schier, A.F. (2017). Nodal patterning without Lefty inhibitory feedback is functional but fragile. eLife 6. 10.7554/eLife.28785.

(11) Thisse, B., Wright, C.V., and Thisse, C. (2000). Activin- and Nodal-related factors control antero-posterior patterning of the zebrafish embryo. Nature 403, 425-428. 10.1038/35000200.

(12) Eroglu, B., Wang, G., Tu, N., Sun, X., and Mivechi, N.F. (2006). Critical role of Brg1 member of the SWI/SNF chromatin remodeling complex during neurogenesis and neural crest induction in zebrafish. Developmental dynamics : an official publication of the American Association of Anatomists 235, 2722-2735. 10.1002/dvdy.20911.

(13) Hensley, M.R., Emran, F., Bonilla, S., Zhang, L., Zhong, W., Grosu, P., Dowling, J.E., and Leung, Y.F. (2011). Cellular expression of Smarca4 (Brg1)-regulated genes in zebrafish retinas. BMC developmental biology 11, 45. 10.1186/1471-213X-11-45.

(14) Kawamura, A., Koshida, S., Hijikata, H., Ohbayashi, A., Kondoh, H., and Takada, S. (2005). Groucho-associated transcriptional repressor ripply1 is required for proper transition from the presomitic mesoderm to somites. Developmental cell 9, 735-744. 10.1016/j.devcel.2005.09.021.

(15) Kawamura, A., Koshida, S., and Takada, S. (2008). Activator-to-repressor conversion of T-box transcription factors by the Ripply family of Groucho/TLE-associated mediators. Mol Cell Biol 28, 3236-3244. 10.1128/MCB.01754-07.

(16) Ross, S., Cheung, E., Petrakis, T.G., Howell, M., Kraus, W.L., and Hill, C.S. (2006). Smads orchestrate specific histone modifications and chromatin remodeling to activate transcription. EMBO J 25, 4490-4502. 10.1038/sj.emboj.7601332.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors aimed to elucidate the recruitment order and assembly of the Cdv proteins during Sulfolobus acidocaldarius archaeal cell division using a bottom-up reconstitution approach. They employed liposome-binding assays, EM, and fluorescence microscopy with in vitro reconstitution in dumbbellshaped liposomes to explore how CdvA, CdvB, and the homologues of ESCRT-III proteins (CdvB, CdvB1, and CdvB2) interact to form membrane remodeling complexes.

The study sought to reconstitute the Cdv machinery by first analyzing their assembly as two subcomplexes: CdvA:CdvB and CdvB1:CdvB2ΔC. The authors report that CdvA binds lipid membranes only in the presence of CdvB and localizes preferentially to membrane necks. Similarly, the findings on CdvB1:CdvB2ΔC indicate that truncation of CdvB2 facilitates filament formation and enhances curvature sensitivity in interaction with CdvB1. Finally, while the authors reconstitute a quaternary CdvA:CdvB:CdvB1:CdvB2 complex and demonstrate its enrichment at membrane necks, the mechanistic details of how these complexes drive membrane remodeling by subcomplexes removal by the proteasome and/or CdvC remain speculative.

Although the work highlights intriguing similarities with eukaryotic ESCRT-III systems and explores unique archaeal adaptations, the conclusions drawn would benefit from stronger experimental validation and a more comprehensive mechanistic framework.

Strengths:

The study of machinery assembly and its involvement in membrane remodeling, particularly using bottom-up reconstituted in vitro systems, presents significant challenges. This is particularly true for systems like the ESCRT-III complex, which localizes uniquely at the lumen of membrane necks prior to scission. The use of dumbbell-shaped liposomes in this study provides a promising experimental model to investigate ESCRT-III and ESCRT-III-like protein activity at membrane necks.

The authors present intriguing evidence regarding the sequential recruitment of ESCRT-III proteins in crenarchaea-a close relative of eukaryotes. This finding suggests that the hierarchical recruitment characteristic of eukaryotic systems may predate eukaryogenesis, which is a significant and exciting contribution. However, the broader implications of these findings for membrane remodeling mechanisms remain speculative, and the study would benefit from stronger experimental validation and expanded contextualization within the field.

We thank the Referee for his/her appreciation of our work.

Weaknesses:

This manuscript presents several methodological inconsistencies and lacks key controls to validate its claims. Additionally, there is insufficient information about the number of experimental repetitions, statistical analyses, and a broader discussion of the major findings in the context of open questions in the field.

We have now added more controls, information about repetitions, and discussion.

Reviewer #2 (Public review):

Summary:

The Crenarchaeal Cdv division system represents a reduced form of the universal and ubiquitous ESCRT membrane reverse-topology scission machinery, and therefore a prime candidate for synthetic and reconstitution studies. The work here represents a solid extension of previous work in the field, clarifying the order of recruitment of Cdv proteins to curved membranes.

Strengths:

The use of a recently developed approach to produce dumbbell-shaped liposomes (De Franceschi et al. 2022), which allowed the authors to assess recruitment of various Cdv assemblies to curved membranes or membrane necks; reconstitution of a quaternary Cdv complex at a membrane neck.

We thank the Referee for his/her appreciation of the work.

Weaknesses:

The manuscript is a bit light on quantitative detail, across the various figures, and several key controls are missing (CdvA, B alone to better interpret the co-polymerisation phenotypes and establish the true order of recruitment, for example) - addressing this would make the paper much stronger. The authors could also include in the discussion a short paragraph on implications for our understanding of ESCRT function in other contexts and/or in archaeal evolution, as well as a brief exploration of the possible reasons for the discrepancy between the foci observed in their liposome assays and the large rings observed in cells - to better serve the interests of a broad audience.

We have now added more controls, information about repetitions, and discussion.

Reviewer #3 (Public review):

Summary:

In this report, De Franceschi et al. purify components of the Cdv machinery in archaeon M. sedula and probe their interactions with membrane and with one-another in vitro using two main assays - liposome flotation and fluorescent imaging of encapsulated proteins. This has the potential to add to the field by showing how the order of protein recruitment seen in cells is related to the differential capacity of individual proteins to bind membranes when alone or when combined.

Strengths:

Using the floatation assay, they demonstrate that CdvA and CdvB bind liposomes when combined. While CdvB1 also binds liposomes under these conditions, in the floatation assay, CdvB2 lacking its C-terminus is not efficiently recruited to membranes unless CdvAB or CdvB1 are present. The authors then employ a clever liposome assay that generates chained spherical liposomes connected by thin membrane necks, which allows them to accurately control the buffer composition inside and outside of the liposome. With this, they show that all four proteins accumulate in necks of dumbbell-shaped liposomes that mimic the shape of constricting necks in cell division. Taken altogether, these data lead them to propose that Cdv proteins are sequentially recruited to the membrane as has also been suggested by in vivo studies of ESCRT-III dependent cell division in crenarchaea.

We thank the Referee for his/her appreciation of the work.

Weaknesses:

These experiments provide a good starting point for the in vitro study the interaction of Cdv system components with the membrane and their consecutive recruitment. However, several experimental controls are missing that complicate their ability to draw strong conclusions. Moreover, some results are inconsistent across the two main assays which make the findings difficult to interpret:

(1) Missing controls.

Various protein mixtures are assessed for their membrane-binding properties in different ways. However, it is difficult to interpret the effect of any specific protein combination, when the same experiment is not presented in a way that includes separate tests for all individual components. In this sense, the paper lacks important controls. For example, Fig 1C is missing the CdvB-only control. The authors remark that CdvB did not polymerise (data not shown) but do not comment on whether it binds membrane in their assays. In the introduction, Samson et al., 2011 is cited as a reference to show that CdvB does not bind membrane. However, here the authors are working with protein from a different organism in a different buffer, using a different membrane composition and a different assay. Given that so many variables are changing, it would be good to present how M. sedula CdvB behaves under these conditions.

We thank the referee for raising this point. We have now added these data in Figure 1C. Indeed it turns out that CdvB from M. sedula exhibits clear membrane binding on its own in a flotation assay.

Similarly, there is no data showing how CdvB alone or CdvA alone behave in the dumbbell liposome assay.

Without these controls, it's impossible to say whether CdvA recruits CdvB or the other way around. The manuscript would be much stronger if such data could be added.

We have now added these data in Figure 1E, 1F and 1G. Overall, we can confirm that CdvA binds the membrane better in the presence of CdvB (although both proteins can bind the membrane on their own). Both proteins appear to recognize the curved region of the membrane neck.

(2) Some of the discrepancies in the data generated using different assays are not discussed.

The authors show that CdvB2∆C binds membrane and localizes to membrane necks in the dumbbell liposome assay, but no membrane binding is detected in the flotation assay. The discrepancy between these results further highlights the need for CdvB-only and CdvA-only controls.

We have now added these controls in Figure 1. In addition, we would like to clarify that the flotation assay and the SMS dumbbell assay serve different purposes and are not directly comparable in quantitative terms. In the flotation assay, all the protein present as input is eventually recovered and visualized. Thus, quantitative information on the proportion of the fraction of the total protein bound to lipids can be inferred from this assay. The SMS assay, in contrast, provides a very different kind of information. Because of the particular protocol required to generate dumbbells (De Franceschi, 2022), the total amount of protein in the inner buffer in dumbbells is not accurately defined, because protein that is not correctly reconstituted (e.g. which aggregates while still in the droplet phase) will interfere with vesicle generation, with the result that dumbbell with such aggregates is generally not formed in the first place. This renders it impossible to draw any quantitative conclusions about the proportion of the sample bound to lipids. The SMS is therefore not directly comparable to the flotation assay, and it is rather complementary to it. Indeed, the purpose of the SMS is to provide information about curvature selectivity of the protein.

(3) Validation of the liposome assay.

The experimental setup to create dumbbell-shaped liposomes seems great and is a clever novel approach pioneered by the team. Not only can the authors manipulate liposome shape, they also state that this allows them to accurately control the species present on the inside and outside of the liposome. Interpreting the results of the liposome assay, however, depends on the geometry being correct. To make this clearer, it would seem important to include controls to prove that all the protein imaged at membrane necks lie on the inside of liposomes. In the images in SFig3 there appears to be protein outside of the liposome. It would also be helpful to present data to show test whether the necks are open, as suggested in the paper, by using FRAP or some other related technique.

We thank the Referee for his/her appreciation. The proteins are encapsulated inside the liposomes, not outside of them. While Figure S3 might give the appearance that there is some protein outside, this is actually just an imaging artifact. Author response image 1 (below) explains this: When the membrane and protein channel are shown separately, it is clear that the protein cluster that appeared to be ‘outside’ actually colocalizes with an extra small dumbbell lobe (yellow arrowhead). The protein appeared to be outside of it because (1) the protein fluorescent signal is stronger than the signal from the membrane, and (2) there is a certain time delay in the acquisition of the two channels (0.5-1 second), thus the membrane may have slightly shifted out of focus when the fluorescence was being acquired. We are confident that the protein is inside in these dumbbells because the procedure for preparing the dumbbells requires extensive emulsification by pipetting, which requires ≈ 1 minute. This time is more than sufficient for proteins with high affinity for the membrane, like ESCRT and Cdv, to bind the membrane. For an example of how fast binding under confinement can be, please see movie 2 from this paper: De Franceschi N, Alqabandi M, Miguet N, Caillat C, Mangenot S, Weissenhorn W, Bassereau P. The ESCRT protein CHMP2B acts as a diffusion barrier on reconstituted membrane necks. J Cell Sci. 2018 Aug 3;132(4):jcs217968.

Moreover, in many instances, we observed that the protein is inside because, by increasing the gain in the images post-acquisition, a clear protein signal appear in the lumen (see Author response image 2).

Author response image 1.

Separate channels showing colocalization of protein and lipids (adapted from Figure S3). The zoom-in shows separate channels, highlighting that the CdvB2 cluster that seems to be ‘outside the dumbbell’ actually colocalizes with the small terminal lobe of the dumbbell, indicating that the protein is encapsulated within that lobe.

Author response image 2.

Residual protein present inside lumen of dumbbells as visualized by increasing the brightness post-acquisition.

We are not sure what the referee means by “test whether the necks are open, as suggested in the paper”. We are confident that the lobes of dumbbells originated from a single floppy vesicle, and were therefore mutually connected with an open neck (at least at the onset of the experiment). We have performed extensive FRAP assays on dumbbells in previous papers (De Franceschi et al., ACS nano 2022 and De Franceschi et al., Nature Nanotech 2024) which unequivocally proved that these chains of dumbbells are connected with open necks. We now also performed a few FRAP assay with reconstituted Cdv proteins, which confirmed this point. We have added a movie of such an experiment to the manuscript (Movie 1).

Investigating whether the necks are open or closed after Cdv reconstitution is indeed a very relevant question, that could be rephrased as “verify whether Cdv proteins or their combination can induce membrane scission”. This is however beyond the scope of this manuscript, as the current work merely addressed the question of hierarchical recruitment of Cdv proteins at the membrane. We plan to examine this in future work.

(4) Quantification of results from the liposome assay.

The paper would be strengthened by the inclusion of more quantitative data relating to the liposome assay. Firstly, only a single field of view is shown for each condition. Because of this, the reader cannot know whether this is a representative image, or an outlier? Can the authors do some quantification of the data to demonstrate this? The line scan profiles in the supplemental figures would be an example of this, but again in these Figures only a single image is analyzed.

The images that we showed are indeed representative. The dumbbells that are generated by the SMS approach contain an “internal control”: in each dumbbell, the protein has the option of localizing at the neck or localizing elsewhere in the region of flat membrane. We see consistently that Cdv proteins have a strong preference for localizing at the neck.

We would recommend that the authors present quantitative data to show the extent of co-localization at the necks in each case. They also need a metric to report instances in which protein is not seen at the neck, e.g. CdvB2 but not CdvB1 in Fig2I, which rules out a simple curvature preference for CdvB2 as stated in line 182.

While the request for better quantitation is reasonable, this would require carrying out very significant new experiments at the microscope, which is rendered near-impossible since both first authors left the lab on to new positions.

Secondly, the authors state that they see CdvB2∆C recruited to the membrane by CdvB1 (lines 184-187, Fig 2I). However, this simple conclusion is not borne out in the data. Inspecting the CdvB2∆C panels of Fig 2I, Fig3C, and Fig3D, CdvB2∆C signal can be seen at positions which don't colocalize with other proteins. The authors also observe CdvB2∆C localizing to membrane necks by itself (Fig 2E). Therefore, while CdvB1 and CdvB2∆C colocalize in the flotation assay, there is no strong evidence for CdvB2∆C recruitment by CdvB1 in dumbbells. This is further underscored by the observation that in the presented data, all Cdv proteins always appear to localize at dumbbell necks, irrespective of what other components are present inside the liposome. Although one nice control is presented (ZipA), this suggests that more work is required to be sure that the proteins are behaving properly in this assay. For example, if membrane binding surfaces of Cdv proteins are mutated, does this lead to the accumulation of proteins in the bulk of the liposome as expected?

In the particular example of Figure 2I, it indeed appears that there are some clusters of CdvB2ΔC that do not contain CdvB1 (we indicated them in Author response image 3 by red arrowheads), while the yellow arrowheads indicate clusters that contain both proteins. It can be clearly seen that the clusters that do contain both proteins (yellow arrows) are localized at necks, while those that only contain CdvB2ΔC (red arrows) are not localized at necks. This is no coincidence. The clusters indicated by the red arrow do contain CdvB1. However, these clusters rapidly diffuse on the membrane plane because they are not fixed at the neck: therefore, they constantly shift in and out of focus. Because there is a time delay in the acquisition of each channel (between 0.5 and 1 second), these cluster were in focus when the CdvB2ΔC signal was being acquired, but sifted out of focus when the CdvB1 signal was being acquired. This implies that the clusters indicated by the yellow arrowheads are stably localized at necks, which is precisely the point we wished to make with this experiment: because Cdv proteins have an affinity for curved geometry, they preferentially and stably localize at necks. Why don’t all the clusters localize at necks then? We estimate that the simple answer is that, in this particular case, there are more clusters than there are necks, so some of the clusters must necessarily localize somewhere else.

Author response image 3.

Current Figure 2H, where clusters that are double-positive for both CdvB1 and CdvB2ΔC are indicated by yellow arrowheads, while cluster that apparently only contain CdvB2ΔC are indicated by red arrowheads. It is observed that all the double-positive clusters are localized at necks.

(5) Rings.

The authors should comment on why they never observe large Cdv rings in their experiments. In crenarchaeal cell division, CdvA and CdvB have been observed to form large rings in the middle of the 1 micron cell, before constriction. Only in the later stages of division are the ESCRTs localized to the constricting neck, at a time when CdvA is no longer present in the ring. Therefore, if the in vitro assay used by the authors really recapitulated the biology, one would expect to see large CdvAB rings in Figs 1EF. This is ignored in the model. In the proposed model of ring assembly (line 252), CdvAB ring formation is mentioned, but authors do not discuss the fact that they do not observe CdvAB rings - only foci at membrane necks. The discussion section would benefit from the authors commenting on this.

The referee is correct: it is intriguing that we don’t see micron-sized rings for CdvA and CdvB. We do note that our EM data (Fig.S1) show that CdvA in its own can form rings of about 100-200nm diameter, well below the diffraction limit, that could well correspond to the foci that we optically resolve in Figure 1. We now added a brief comment on this to the manuscript on lines 256-264.

(6) Stoichiometry

It is not clear why 100% of the visible CdvA and 100% of the the visible CdvB are shifted to the lipid fraction in 1C. Perhaps this is a matter of quantification. Can the authors comment on the stoichiometry here?

We agree that this was unclear. Since that particular gel was stained by coumassie, the quantitative signals might be unreliable, and hence we have repeated this experiment using fluorescently labelled proteins, which show indeed a less extreme distribution. This was also done to make the data more uniform, as requested by the referees.

(7) Significance of quantification of MBP-tagged filaments.

Authors use tagging and removal of MBP as a convenient, controllable system to trigger polymerisation of various Cdv proteins. However, it is unclear what is the value and significance of reporting the width and length of the short linear filaments that are formed by the MBP-tagged proteins. Presumably they are artefactual assemblies generated by the presence of the tag?

Providing a measure of the changes induced by MBP removal, in fact, validates that this actually has an effect. But perhaps this places too much emphasis on the short filaments. We now opted for a compromise, removing the quantification of the width and length of short filaments formed by MBPtagged protein from the text, but keeping the supplementary figure showing their distribution as compared to the other filaments (Figure S2E, SF).

Similar Figure 2C doesn't seem a useful addition to the paper.

We removed panel 2C, and now merely report these values in the text.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

I would suggest the authors perform a deeper discussion about their findings, such as what are the evolutionary implications, how they think lipids from these archaea may affect the recruitment process,...

Because there is no exact homology between Archaea Cdv proteins and Eukaryotic ESCRT-III proteins, we do not feel our work brings new evolutionary implications beyond what we already state in the manuscript. We also dis not perform experiments using Archaea lipids, thus we would rather not speculate on how they may potentially affect the recruitment of Cdv proteins.

In general, the manuscript lacks information regarding some scale bars, number of experimental repetitions (n or N), statistical analysis when needed, information about protein concentrations used in their assays.

We have now added this information in the manuscript.

Below, I provide a list of comments that I think the authors should address to improve the manuscript:

(1) Line 113-114: The authors test protein-membrane interactions using flotation assays with positively curved SUV membranes but encapsulate proteins in dumbbell-shaped liposomes with negative curvature at the connecting necks. Might the use of membranes with opposite curvatures affect the recruitment process? Since the proteins are fluorescently labeled, I suggest testing recruitment using flat giant unilamellar vesicles or supported lipid bilayers (with zero curvature) to validate their findings.

We thank the referee for this suggestion. Please do note that we are not claiming in our paper that Cdv proteins recognize negative curvature. We merely observe that they localize at necks. The neck of a dumbbell exhibits the so-called “catenoid” geometry, which is characterized by having both positive and negative curvature.

Experimentally, on the SUVs, we now realize there was a mistake in the method section: In the flotation assay we in fact used multilamellar vesicles, not SUVs, precisely for the reason mentioned by the referee. We apologize for the oversight and have now corrected this in the methods. Multilamellar vesicles are not characterized by a strong positive curvature as SUVs do, but we do agree that they likely don’t have negative curvature there either. Because of the heterogeneous nature of the multilamellar vesicles, they provide a binding assay that was rather independent of the curvature. Complementary to the flotation assay, the SMS approach was employed to reveal the curvature preference of proteins.

Finally, we performed the experiment on large GUVs suggested by the referee using CdvB as an example, but this turned out to be inconclusive because the protein forms clusters: these clusters may be creating local curvature at the nanometer scale, which cannot be resolved by optical microscopy (Author response image 4). This is quite typical for proteins that recognize curvature (cf. for instance: De Franceschi N, Alqabandi M, Miguet N, Caillat C, Mangenot S, Weissenhorn W, Bassereau P. The ESCRT protein CHMP2B acts as a diffusion barrier on reconstituted membrane necks. J Cell Sci. 2018 Aug 3;132(4):jcs217968.)

Author response image 4.

Fluorescently labelled CdvB bound to giant unilamellar vesicle. The protein was added in the outer buffer. CdvB forms distinct clusters, which may generate a local region of high membrane curvature.

(2) Line 138-139: How is His-ZipA binding the membrane? Wouldn't Ni²⁺-NTA lipids be required? If not, how is the binding achieved?

Indeed, NTA-lipids were present. This is now stated both in the legend and in the methods.

(3) In the encapsulated protein assays, why does the luminal fluorescence intensity of the encapsulated protein sometimes appear similar to the bulk fluorescence signal? Since only a small fraction of the protein assembles at membrane necks, shouldn't the luminal pool of unbound protein show higher fluorescence intensity inside the liposomes?

We thank the referee for raising this point and giving us the opportunity to explain this. The reason is that Cdv proteins have a very high affinity for the neck, and when they cluster at the neck the fluorescence intensity of the cluster is many times higher than the background fluorescence. Because we were interested in imaging the clusters and avoiding overexposing them, we adjusted the imaging conditions accordingly, with the result that the fluorescence from both the lumen and the bulk is at very low level.

By choosing different imaging conditions, however, it can be actually seen that the signal inside the lumen is clearly higher than the bulk: this can be seen for instance in Author response image 2, where the brightness has been properly adjusted.

(4) Line 184-185: In Fig. 2I, some CdvB2ΔC puncta seem independent of CdvB1 and are not localized at membrane necks. How many such puncta exist? For example, in the provided micrograph, 2 out of 5 clusters are independent of CdvB1. This proportion is significant. Could the authors quantify the prevalence of these structures and discuss why they form?

We thank the referee for giving us the opportunity to explain this apparent discrepancy. We’ll like to stress the fact that CdvB2ΔC and CdvB1 form an obligate heterodimer: in all our experiments, without exception, we find that they form a strong complex when we mix the two proteins. This is true both in dumbbells and in flotation assays.

In the particular example of Figure 2I, it indeed appears that there are some clusters of CdvB2ΔC that do not contain CdvB1 (we indicated them in Author response image 3 by red arrowheads), while the yellow arrowheads indicate clusters that contain both proteins. It can be clearly seen that the clusters that do contain both proteins (yellow arrows) are localized at necks, while those that only contain CdvB2ΔC (red arrows) are not localized at necks. This is no coincidence. The clusters indicated by the red arrow do contain CdvB1. However, these clusters rapidly diffuse on the membrane plane because they are not fixed at the neck: therefore, they constantly shift in and out of focus. Because there is a time delay in the acquisition of each channel (between 0.5 and 1 second), these cluster were in focus when the CdvB2ΔC signal was being acquired, but sifted out of focus when the CdvB1 signal was being acquired. This implies that the clusters indicated by the yellow arrowheads are stably localized at necks, which is precisely the point we wished to make with this experiment: because Cdv proteins have affinity for curved geometry, they preferentially and stably localize at necks. Why don’t all the clusters localize at necks then?

(5) Figure 1E and 1F: Why do lipids accumulate and colocalize with the proteins? How can the authors confirm lumen connectivity between vesicles? Performing FRAP assays could validate protein localization and enrichment at the lumen of the membrane necks.

At first sight, indeed some lipid enrichment seems to be observed at the neck between lobes of dumbbells.

This is, however, an imaging artifact due to the fact that the neck is diffraction limited. As shown in the Author response image 5, we are acquiring the membrane signal from both lobes at the neck region, and therefore the signal is roughly double, hence the apparent lipid enrichment.

Author response image 5.

Schematic illustrating that the neck between two lobes is smaller than the diffraction limit of optical microscopy (the size of a typical pixel is indicated by the green square). Because of this technical limitation, the fluorescence intensity of the membrane at the neck is twice that of a single membrane.

The referee is correct in pointing out that these images do not prove that the lobes are connected, and that FRAP assays is the only way to prove this point. However, in previous papers we have confirmed extensively that in chains of dumbbells the lobes are connected:

- De Franceschi N, Pezeshkian W, Fragasso A, Bruininks BMH, Tsai S, Marrink SJ, Dekker C. Synthetic Membrane Shaper for Controlled Liposome Deformation. ACS Nano. 2022 Nov 28;17(2):966–78. doi: 10.1021/acsnano.2c06125.

- De Franceschi N, Barth R, Meindlhumer S, Fragasso A, Dekker C. Dynamin A as a one-component division machinery for synthetic cells. Nat Nanotechnol. 2024 Jan;19(1):70-76. doi: 10.1038/s41565023-01510-3.

Random sticking of liposomes would also generate clusters of vesicles, not linear chains. We now provide also a Movie (Movie 1) supporting this point.

Investigating whether the necks are open or closed after Cdv reconstitution is indeed a very relevant question, that could be rephrased as “verify whether Cdv proteins or their combination can induce membrane scission”. This is however beyond the scope of this manuscript, as the current work merely addressed the question of hierarchical recruitment of Cdv proteins at the membrane. We plan to examine this in future work.

(6) Why didn't the authors use the same lipid composition, particularly the same proportion of negatively charged lipids, on the SUVs of the flotation assays and on the dumbbell-shaped liposomes?

In flotation assays, it is typical to use a relatively large proportion of negatively charged lipids, to promote protein binding. This is because the aim is to maximize membrane coverage by the protein. The SMS procedure to generate dumbbell-shaped GUVs is completely different, however. Rather than covering the membrane with protein, the idea is to reduce the amount of protein to a minimum, so that any curvature preference can be best visualized. This is e.g. routinely done in tube pulling experiments, for the same reason (See for instance Prévost C, Zhao H, Manzi J, Lemichez E, Lappalainen P, Callan-Jones A, Bassereau P. IRSp53 senses negative membrane curvature and phase separates along membrane tubules. Nat Commun. 2015 Oct 15;6:8529. doi: 10.1038/ncomms9529).

(7) Line 117-119: The suggestion that polymer formation between CdvA and CdvB facilitates membrane recruitment is intriguing. However, fluorescence microscopy experiments could better elucidate whether there is sequential recruitment of CdvB followed by CdvA, or if these proteins form a heteropolymer composite for membrane binding. Can CdvB bind membranes independently, or does this require synergy between CdvA and CdvB.

We thank the referee for prompting us to perform this experiment. As we now show in Figure 1C, CdvB indeed is able to bind the membrane independently of CdvA. Whether this happens sequentially or simultaneously is an interesting question, but one that is impossible to address with either the SMS or the flotation assay, because in both cases we can only observe the endpoint of the recruitment.

We would also like to clarify one specific experimental detail. Perhaps unsurprisingly, the results from the flotation assay are dependent on the way the assay is performed. In particular, we observed that the same protein can exhibit a different binding profile depending on whether it is being loaded either at the top or at the bottom of the gradient. This can be seen in Author response image 6. This is counterintuitive, since once the equilibrium is reached, the result should only depend on the density of the sample. We performed an overnight centrifugation (> 16 hours) on a short tube (< 3 cm tall), thus equilibrium is being reached (which is corroborated by the fact that CdvB1 and CdvB2 can float to the top of the gradient within this timespan, as shown in Figure 2C, 2E, 2G). We ascribe the difference between top and bottom loading to the fact that, when the sample is loaded at the bottom, it has to be mixed with a concentrated sucrose solution, while in the case of loading from the top, this is not done.

In literature, both loading from top and from bottom have been used:

- Lata S, Schoehn G, Jain A, Pires R, Piehler J, Gottlinger HG, Weissenhorn W. Helical structures of ESCRTIII are disassembled by VPS4. Science. 2008 Sep 5;321(5894):1354-7. doi: 10.1126/science.1161070

- Moriscot C, Gribaldo S, Jault JM, Krupovic M, Arnaud J, Jamin M, Schoehn G, Forterre P, Weissenhorn W, Renesto P. Crenarchaeal CdvA forms double-helical filaments containing DNA and interacts with ESCRT-III-like CdvB. PLoS One. 2011;6(7):e21921. doi: 10.1371/journal.pone.0021921.

- Senju Y, Lappalainen P, Zhao H. Liposome Co-sedimentation and Co-flotation Assays to Study LipidProtein Interactions. Methods Mol Biol. 2021;2251:195-204. doi: 10.1007/978-1-0716-1142-5_14. In performing the flotation assay for CdvB1 and CdvB2ΔC, or when using all 4 proteins together, we loaded the sample at the bottom, and we could detect reproducible binding to liposomes (Figures 2D, 2F, 2H, 3A). However, CdvB does not bind the membrane when loaded at the bottom. Thus, for the experiments shown in figure 1C, we loaded the proteins at the top. This experimental setup allowed us to highlight that CdvB indeed induce a stronger interaction between CdvA and the membrane.

Author response image 6.

CdvB binding to multilamellar vesicles in a flotation assay. In the left panel, the sample was loaded at the top of the sucrose gradient; in the right panel it was loaded at the bottom.

(8) Line 165-173: The authors claim that filament curvature differs between CdvB2ΔC alone and the CdvB1:CdvB2ΔC complex. Are these differences statistically significant? What is the sample size (N)? Furthermore, how do the authors confirm interactions between these proteins in the absence of membranes based solely on EM micrographs?

We can confirm that the filaments are composed by both proteins, because the filaments have different curvature when both proteins are present. However, as requested by referee 3, point (7), we removed the quantification of curvature from panel 2C. We report the N number in the text.

(9) Line 121-123: Are the authors referring to positive or negative membrane curvatures? The cited literature suggests ESCRT-III proteins either lack curvature preferences (e.g., Snf7, CHMP4B) or prefer high positive curvature (e.g., late ESCRT-III subunits). This is confusing since the authors later test recruitment to negatively curved necks.

We do not claim that Cdv proteins prefer positive or negative curvature, because the necks present in dumbbells have a catenoid geometry, which include both positive and negative curvature. We have now clarified this in the discussion.

(10) Since the conclusions rely on the oligomeric state of the proteins, providing SEC-MALS spectra to show the protein oligomeric state right after the purification would strengthen the claims.

While such SEC-MALDI experiments may be interesting, practical implementation of this is not possible since both first authors left the lab on to new positions.

(11) Line 157-160: Suppl. Fig. 2 shows only a single EM micrograph of a small filament. Could the authors provide lower magnification images showing more filaments?

As requested by Referee 3, point (7), we have toned down the importance of these short filaments.

Also, why are the sample sizes for filament length (N=161) and width (N=129) different?

Protein filaments formed by Cdv tend to stick to each other side by side, so that for some filaments the width could not be accurately assessed, and accordingly those were removed from the analysis.

(12) The introduction states that CdvA binds membranes while CdvB does not. However, the results suggest CdvB facilitates membrane binding, helping CdvA attach. This discrepancy needs further explanation.

We thank the referee for raising this point. We have now performed additional experiments (both SMS assay and flotation assays) showing that indeed CdvB from M. sedula is (unlike CdvB from Sulfolobus) able to bind the membrane on its own (Figure 1C, 1F).

Reviewer #2 (Recommendations for the authors):

Best practice would be to show single fluorescence channels in grayscale or inverted grayscale, retaining pseudocolouring only for the merged multichannel image.

We decided to retain and standardize the colors, both for gels and for microscopy images, in order to have the same color-code for each protein. We believe this improves readability, and this was also a request from Referee 3. Thus, throughout the manuscript, CdvA is in grayscale, CdvB in yellow, CdvB1 in green, CdvB2ΔC in cyan and the membrane in magenta.

It would be great to include a quantification of liposome curvature vs focal intensity of the various Cdv components - across figures.

Quantification of liposome curvature at the neck can be done (De Franceschi et al., Nature Nanotech. 2024). However, in practice, this requires transferring of the sample post-preparation into a new chamber in order to increase the signal-to-noise ratio of the encapsulated dye, a procedure that drastically reduces the yield of dumbbells. The very sizeable amount of work required to obtain reliable measurements, especially considering all the proteins and protein combinations used in this study, indicates that this represents a project in itself, which goes well beyond the scope of this manuscript.

Reviewer #3 (Recommendations for the authors):

(1) We would encourage the authors to consider including the length of the scale bar next to the scale bar in each image and not in the figure description. This would greatly aid in clarity and interpretation of figures.

We have now written the length of the scale bar in the figures.

(2) In a similar vein, could the authors consider labeling panels throughout the manuscript, writing that sample is being presented? This goes mainly for the negative stain and the dumbbell fluorescence images, as having to continuously consult the figure legend again hinders clarity.

We have now labelled the EM images as requested by the referee.

(3) Lines 254-256: would the statement hold not only for CdvB2∆C, but for all imaged proteins? They all seem to localize to membrane necks, presumably favoring membrane binding to a specific membrane topology.

We agree with the referee, and changed the phrasing accordingly.

(4) CdvB2∆C construct - presumably this was a truncation of helix 5 of the ESCRT-III domain? Figure 1A shows that the ESCRT-III domain spans residues 34-170 and therefore implies that all five ESCRT-III helices (which make up the ESCRT-III domain) are present in the C-terminal truncation. Could the authors clarify?

Indeed, the truncation was done at residue 170.

(5) Results of the liposome flotation assays are presented inconsistently across the three figures (Figs 1C, 2DFH, and 3A). This makes it more difficult than it needs to be to interpret and compare results. Could the authors consider presenting the three gels in a more similar, standardized way across the three figures?

To improve readability, we now standardized the colors, both for gels and for microscopy images, in order to have the same color-code for each protein. Thus, throughout the manuscript, CdvA is in grayscale, CdvB in yellow, CdvB1 in green, CdvB2ΔC in cyan and the membrane in magenta.

(6) From the data presented in Fig 1EF, it cannot be concluded whether CdvB and CdvA colocalize, as only one protein is labelled. Is there a technical reason for this?

We have now repeated the same experiment by having both proteins labelled, confirming that there is co-localization at the neck (Figure 1G).

(7) Fig 2C: is the difference between the two samples significant

As requested by Referee 3, we have removed Figure 2C.

(8) Fig 2I is missing a 'merged' panel.

We have now added the merged panel.

(9) The fluorescence intensity plots in Supp Figs 1C and 3C would be easier to interpret if the lipid and protein signal would be plotted on the same plot (say, with normalized fluorescence intensity)

It is not immediately obvious to us what the signal should be normalized to. What we wished to convey with these plots was that the intensity of proteins spikes at the neck region. In an attempt to improve clarity, we have now aligned the plots vertically, and highlighted the position of the neck.

(10) CdvA should have a capital "A" in Figure 3A, panel 3.

We have now corrected this.

(11) The discussion doesn't comment on the need to truncate CdvB2.

This is explained in the result session.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Kroeg et al. describe a novel method for 2D culture human induced pluripotent stem cells (hiPSCs) to form cortical tissue in a multiwell format. The method claims to offer a significant advancement over existing developmental models. Their approach allows them to generate cultures with precise, reproducible dimensions and structure with a single rosette; consistent geometry; incorporating multiple neuronal and glial cell types (cellular diversity); avoiding the necrotic core (often seen in free-floating models due to limited nutrient and oxygen diffusion). The researchers demonstrate the method's capacity for long-term culture, exceeding ten months, and show the formation of mature dendritic spines and considerable neuronal activity. The method aims to tackle multiple key problems of in vitro neural cultures: reproducibility, diversity, topological consistency, and electrophysiological activity. The authors suggest their potential in high-throughput screening and neurotoxicological studies.

Strengths:

The main advances in the paper seem to be: The culture developed by the authors appears to have optimal conditions for neural differentiation, lineage diversification, and long-term culture beyond 300 days. These seem to me as a major strength of the paper and an important contribution to the field. The authors present solid evidence about the high cell type diversity present in their cultures. It is a major point and therefore it could be better compared to the state of the art. I commend the authors for using three different IPS lines, this is a very important part of their proof. The staining and imaging quality of the manuscript is of excellent quality.

We thank the reviewer for the positive comments on the potential of our novel platform to address key problems of in vitro neural culture, highlighting the longevity and reproducibility of the method across multiple cell lines.

Weaknesses:

(1) The title is misleading: The presented cultures appear not to be organoids, but 2D neural cultures, with an insufficiently described intermediate EB stage. For nomenclature, see: doi: 10.1038/s41586-022-05219-6. Should the tissue develop considerable 3D depth, it would suffer from the same limited nutrient supply as 3D models - as the authors point out in their introduction.

We appreciate the opportunity to clarify this point. We respectfully disagree that the cultures do not meet the consensus definition of an organoid. In fact, a direct quote from the seminal nomenclature paper referenced by the reviewer states: “We define organoids as in vitro-generated cellular systems that emerge by self-organization, include multiple cell types, and exhibit some cytoarchitectural and functional features reminiscent of an organ or organ region. Organoids can be generated as 3D cultures or by a combination of 3D and 2D approaches (also known as 2.5D) that can develop and mature over long periods of time (months to years).” (Pasca et al, 2022 doi10.1038/s41586-022-05219-6). Therefore, while many organoid types indeed have a more spherical or globular 3D shape, the term organoid also applies to semi-3D or nonglobular adherent organoids, such as renal (Czerniecki et al 2018, doi.org/10.1016/j.stem.2018.04.022) and gastrointestinal organoids (Kakni et al 2022, doi.org/10.1016/j.tibtech.2022.01.006). Accordingly, the adherent cortical organoids described in the manuscript exhibit self-organization to single radial structures consisting of multiple cell layers in the z-axis, reaching ~200um thickness (therefore remaining within the limits for sufficient nutrient supply), with consistent cytoarchitectural topology and electrophysiological activity, and therefore meet the consensus definition of an organoid.

(2) The method therefore should be compared to state-of-the-art (well-based or not) 2D cultures, which seems to be somewhat overlooked in the paper, therefore making it hard to assess what the advance is that is presented by this work.

It was not our intention to benchmark this model quantitatively against other culture systems. Rather, we have attempted to characterize the opportunities and limitations of this approach, with a qualitative contrast to other culture methods. Compared to stateof-the-art 2D neural network cultures, adherent cortical organoids provide distinct advantages in:

(1) Higher order self-organized structure formation, including segregation of deeper and upper cortical layers.

(2) Longevity: adherent cortical organoids can be successfully kept in culture for at least 1 year, whereas 2D cultures typically deteriorate after 8-12 weeks.

(3) Maturity, including the formation of dendritic mushroom spines and robust electrophysiological activity.

(4) Cell type diversity including a more physiological ratio of inhibitory and excitatory neurons (10% GAD67+/NeuN+ neurons in adherent cortical organoids, vs 1% in 2D neural networks), and the emergence of oligodendrocyte lineage cells.

On the other hand, limitations of adherent cortical organoids compared to 2D neural network cultures include:

(1) Culture times for organoids are much longer than for 2D cultures and the method can therefore be more laborious and more expensive.

(2) Whole cell patch clamping is not easily feasible in adherent cortical organoids because of the restrictive geometry of 384-well plates.

(3) Reproducibility is prominently claimed throughout the manuscript. However, it is challenging to assess this claim based on the data presented, which mostly contain single frames of unquantified, high-resolution images. There are almost no systematic quantifications presented. The ones present (Figure S1D, Figure 4) show very large variability. However, the authors show sets of images across wells (Figure S1B, Figure S3) which hint that in some important aspects, the culture seems reproducible and robust.

We made considerable efforts to establish quantitative metrics to assess reproducibility. We applied a quantitative scoring system of single radial structures at different time points for multiple batches of all three lines as indicated in Figure S1C. This figure represents a comprehensive dataset in which each dot represents the average of a different batch of organoids containing 10-40 organoids per batch. To emphasize this, we have adapted the graph to better reflect the breadth of the dataset. Additional quantifications are given in Figure S2 for progenitor and layer markers for Line 1 and in Figure 2 for interneurons across all three lines, showing relatively low variability. That being said, we acknowledge the reviewer’s concerns and have modified the text to reduce the emphasis of this point, pending more extensive data addressing reproducibility across an even broader range of parameters.

(4) What is in the middle? All images show markers in cells present around the center. The center however seems to be a dense lump of cells based on DAPI staining. What is the identity of these cells? Do these cells persist throughout the protocol? Do they divide? Until when? Addressing this prominent cell population is currently lacking.

A more comprehensive characterization of the cells in the center remains a significant challenge due to the high cell density hindering antibody penetration. However, dyebased staining methods such as DAPI and the LIVE/DEAD panel confirm a predominance of intact nuclei with very minimal cell death. The limited available data suggest that a substantial proportion of the cells in the center are proliferative neural progenitors, indicated by immunolabeling for SOX2 (Figure 2A,D;Figure S4C). Furthermore, we are currently optimizing the conditions to perform single cell / nuclear RNA sequencing to further characterize the cellular composition of the organoids.

(5) This manuscript proposes a new method of 2D neural culture. However, the description and representation of the method are currently insufficient. (a) The results section would benefit from a clear and concise, but step-by-step overview of the protocol. The current description refers to an earlier paper and appears to skip over some key steps. This section would benefit from being completely rewritten. This is not a replacement for a clear methods section, but a section that allows readers to clearly interpret results presented later.

We have revised the manuscript to include a more detailed step-by-step overview of the protocol.

(b) Along the same lines, the graphical abstract should be much more detailed. It should contain the time frames and the media used at the different stages of the protocol, seeding numbers, etc.

As suggested, we have adapted the graphical abstract to include more detail.

Reviewer #2 (Public review):

Summary:

In this manuscript, van der Kroeg et al have developed a method for creating 3D cortical organoids using iPSC-derived neural progenitor cells in 384-well plates, thus scaling down the neural organoids to adherent culture and a smaller format that is amenable to high throughput cultivation. These adherent cortical organoids, measuring 3 x 3 x 0.2 mm, self-organize over eight weeks and include multiple neuronal subtypes, astrocytes, and oligodendrocyte lineage cells.

Strengths:

(1) The organoids can be cultured for up to 10 months, exhibiting mature dendritic spines, axonal myelination, and robust neuronal activity.

(2) Unlike free-floating organoids, these do not develop necrotic cores, making them ideal for high-throughput drug discovery, neurotoxicological screening, and brain disorder studies.

(3) The method addresses the technical challenge of achieving higher-order neural complexity with reduced heterogeneity and the issue of necrosis in larger organoids. The method presents a technical advance in organoid culture.

(4) The method has been demonstrated with multiple cell lines which is a strength.

(5) The manuscript provides high-quality immunostaining for multiple markers.

We appreciate the reviewer’s acknowledgement of the strengths of this novel platform as a technical advance in organoid culture that reduces heterogeneity and shows potential for higher throughput experiments.

Weaknesses:

(1) Direct head-to-head comparison with standard organoid culture seems to be missing and may be valuable for benchmarking, ie what can be done with the new method that cannot be done with standard culture and vice versa, ie what are the aspects in which new method could be inferior to the standard.

In our opinion, it would be extremely difficult to directly compare methods. Most notably, whole brain organoids grow to large and irregular globular shapes, while adherent cortical organoids have a more standardized shape confined by the geometry of a 384well. Moreover, it was not our intention to benchmark this model quantitatively against other culture systems. Rather, we have attempted to characterize the opportunities and limitations of this approach, with a qualitative contrast to other culture methods, as addressed in response to comment 2 of Reviewer 1 above.

(2) It would be important to further benchmark the throughput, ie what is the success rate in filling and successfully growing the organoids in the entire 384 well plate?

Figure S1 shows the success rate of organoid formation and stability of the organoid structures over time. In addition, we have added the number of wells that were filled per plate.

(3) For each NPC line an optimal seeding density was estimated based on the proliferation rate of that NPC line and via visual observation after 6 weeks of culture. It would be important to delineate this protocol in more robust terms, in order to enable reproducibility with different cell lines and amongst the labs.

Figure S1 provides the relationship between proliferation rate and seeding density, allowing estimation of seeding densities based on the proliferation rate of the NPCs. However, we appreciate the reviewers' feedback and have modified the methods to provide more detail.

Reviewer #3 (Public review):

Summary:

Kroeg et al. have introduced a novel method to produce 3D cortical layer formation in hiPSC-derived models, revealing a remarkably consistent topography within compact dimensions. This technique involves seeding frontal cortex-patterned iPSC-derived neural progenitor cells in 384-well plates, triggering the spontaneous assembly of adherent cortical organoids consisting of various neuronal subtypes, astrocytes, and oligodendrocyte lineage cells.

Strengths:

Compared to existing brain organoid models, these adherent cortical organoids demonstrate enhanced reproducibility and cell viability during prolonged culture, thereby providing versatile opportunities for high-throughput drug discovery, neurotoxicological screening, and the investigation of brain disorder pathophysiology. This is an important and timely issue that needs to be addressed to improve the current brain organoid systems.

We thank the reviewer for highlighting the strengths of our novel platform. We appreciate that all three reviewers agree that the adherent cortical organoids presented in this manuscript reliably demonstrate increased reproducibility and longevity. They also commend its potential for higher throughput drug discovery and neurotoxicological/phenotype screening purposes.

Weaknesses:

While the authors have provided significant data supporting this claim, several aspects necessitate further characterization and clarification. Mainly, highlighting the consistency of differentiation across different cell lines and standardizing functional outputs are crucial elements to emphasize the future broad potential of this new organoid system for large-scale pharmacological screening.

We appreciate the feedback and have added more detail on consistency and standardization of functional outputs.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Minor points

(1) As the preprint is officially part of the eLife review, I have to remark that the preprint which is made available on bioarxiv, suffers from some serious compatibility or format problem: one cannot highlight sentences as in a regular PDF and when trying to copypaste sentences from it jumbled characters are copied to the clipboard.

The updated version of the paper on bioRxiv should not suffer from these compatibility issues.

(2) Since the paper is presenting a new method it should briefly describe how each step, including the hiPSC culture was done, the reference to an earlier publication in this case is not sufficient, and this practice is generally best to avoid for methods papers.

Each step in the culturing process has now been described in the methods.

(3) The EB stage is insufficiently described. The "2D - 3D - 2D" transitions should be clearly explained.

The methods section has been rewritten and expanded to include these processes in more detail.

(4) Is there one FACS sorting in the protocol, or multiple (additional at IPS culture)? What markers each? What is the motivation for sorting and purifying the neural progenitors? Was the culture impure? What was purity? What cell types are expected after sorting, and what is removed?

Only one FACS sorting step is performed at the NPC stage. This was added as an improvement to our original neural network protocol (Günhanlar et al 2018) to ensure consistency over different hiPSC source cell lines that can yield variable amounts of frontal cortical patterned NPCs. Positive sorting for neural lineage markers CD184 and CD24, and negative sorting for mesenchymal/neural crest CD217 and CD44 glial progenitor markers, according to Yuan et al 2011, ensures frontal-patterned cortical NPCs as confirmed for all batches by immunohistochemistry for SOX2, Nestin and FOXG1. We have added new text to the Methods section to clarify this more explicitly.

(5) Seeding protocol and parameters are insufficiently described, and from what I read they are poorly defined: "Specifically, the optimal seeding density was determined by visual inspection of the organoids between 28 to 42 days after seeding a range of cell densities in the 384-well plate wells." For a new method, precise, actionable instructions are needed. I may have overlooked those elsewhere, in this case, please clarify these sections.

The Methods section was rewritten and expanded to describe the methodology in greater detail with more actionable instructions.

(6) The timeline in Figure 1 is not clearly delineated; I found it hard to understand which figure corresponds to which stage (e.g. facs sorting is not mentioned in the first part of the results but it is part of Figure 1A, neural rosette formation can happen both before and after facs sorting, simply referring to rosettes is not clear). Later parts of the manuscript 
> clearly introduce the terms sorting and seeding in the context of this method, and how ages (days) refer to these time points.

Figure 1 was adapted to clarify the generation of Neural Progenitor Cells (NPCs) and subsequent seeding of NPCs to generate Adherent Cortical Organoids (ACOs).

(7) The authors define: "cortical organized defined as a single radial structure." This is not a commonly used definition of organoids, for nomenclature, please see: doi: 10.1038/s41586-022-05219-6 (Pasca et al 2022).

To clarify, the statement is not meant to reflect a definition of organoids in general, but rather the scoring of proper structure formation for Figure S1C. For discussion on nomenclature, see our response to point 1 of Reviewer 1 in the public review. We changed the wording to be more accurate.

(8) In Figure S1d, the authors write: "the fraction of structurally intact cultures decreased to 50%", but I'm looking at that graph there seems to be no notable decrease, but huge variability. The authors should quantify claims of decrease by linear regression and an R square. Variation within and the cross-cell lines seem to be large. Also, it is unclear if dots are corresponding to the same wells/plates, in other words: is this a longitudinal experiment? What is the overall success rate? How is success determined? Are there clear criteria? to the same wells/plates, in other words: is this a longitudinal experiment? What is the overall success rate? How is success determined? Are there clear criteria?

We agree with the reviewer that the claim on fraction of intact cultures decreasing over time to 50% is an overinterpretation due the large variability. We changed the wording in the manuscript to: While some later batches show moderately reduced success rates compared with the earliest batches, properly formed single-structure organoids were still obtained at 40–90% success across all examined time points (Figure S1C), indicating that long-term culture is feasible albeit with variable efficiency. The data are not longitudinal as each dot represents an endpoint of a different batch of organoids, totaling 18 independent batches across the three lines. We have clarified this in the figure legend. Success was defined at the well level as the presence of a single, continuous radial structure occupying the well, without obvious fragmentation or fusion events, as assessed by LIVE/DEAD that also confirmed viability. Wells were scored as successful only when the radial structure showed predominantly live signal with no large necrotic areas. Wells containing multiple radial structures, fused aggregates, or predominantly dead tissue were scored as unsuccessful.

(9) Figure s1c: the numbering to this panel should be swapped, because it is referenced after other panels in the text. The reference is confusing: "Plotting the interaction between proliferation and the amount of NPCs required to be seeded for the successful generation of adherent cortical organoids" - success is not present in this graph at all? How is that measured?

Figures S1C and S1D have been adapted to clarify the measure of ‘successful organoid formation’.

(a) The description of this plot is confusing: "The doubling time of the NPCs explains more than half the variation (r2 = 0.67) of the required seeding density." What else is there? I thought that this was the formula the authors suggested to determine seeding density, but it seems not. Or is "manual inspection" the determinant, and that seems to correlate with this metric?

Even though the rate of proliferation, measured as doubling time, is the main determinant of the seeding density, it is not the only determinant of the seeding density. For instance, intrinsic differences in differentiation potential could also play a role. Therefore, NPC lines with similar doubling times might still have slightly different optimal seeding densities. We have added clarification of this conclusion to the Results section.

(b) Seeding density is a key parameter in many in vitro differentiation and culture protocols. This importance however does not mean that this density is attributable to differences in cell proliferation rate. Alternatively, the amount of cells determines the amount of secreted molecules and cell-to-cell contacts.

Here, when we refer to the cell density, we specifically refer to the cell density needed to generate the ACO. We show that the most important contributor to the variation in ACO formation is the proliferation, measured here as the doubling time. We agree that there are other factors involved such as the secreted molecules, cell-to-cell contacts as well as the ability of a given NPC line to differentiate into a post-mitotic cell.

(c) Is it mentioned which cell line this experiment corresponds to?

The data in Figure S1D is from the 3 reported cell lines, as well as 2 clones from a fourth IPS cell line. This is detailed in the Methods section of the proliferation assay.

(d) Without a more detailed explanation, seeding density and doubling time could be independent variables.

These two variables are highly correlated as shown in Figure S1D, but it is true that there can be other variables that account for the observed variance, as discussed above in Point 9b.

(e) In this figure the success rate is not visible at all so I have no idea how the autors arrive at a conclusion about success rate.

We have adapted the figure legend to reflect which cell lines the dots in Fig. S1D represent. NPC lines can have substantial variation in proliferation rates. The figure reflects data of NPCs of 5 clones of 4 different hiPSC lines (as indicated in the Methods) with different proliferation rates. Also, the ACO success rate (operationally defined uniformly to the data shown in Fig. S1C) was also included.

(10) Figure 2: Clean spatial segregation seems to be a strength of the system and therefore I would recommend putting more of the relevant microscopy images to the main figure, which are now currently in Figure S4.

We have adapted Figure 2 accordingly, and included additional representative cortical layering images in Figure S4.

(11) The variability in interneuron content seems to be significant, as currently presented in the figure. However, this may be due to a special organization. It would first quantify in consecutive rings around the centers whether interneurons have a tendency to be enriched towards the center or the edge of the culture. Maybe this explains the variability that is currently present in Figure s5b.

We agree that spatial organization of interneurons could, in principle, contribute to variability. In our analysis, however, images were acquired from positions selected by a random sampling grid across the entire culture, rather than from specific central or peripheral regions. Each field contained on average 130.6 ± 16.1 NeuN+ nuclei, which provided a relatively large sampling volume per position. If interneurons were strongly enriched at the center or edge, we would expect systematic differences in interneuron fraction between fields assigned to central versus peripheral grid positions. We did not observe such a pattern in our dataset, suggesting that spatial organization is not the main driver of the observed variability.

(12) Because in previous figures it seems like there is considerable variability across individual cultures and images here are coming from separate cultures, please use different shapes of the points coming from different cultures/wells, to see if maybe there is a culture-to-culture difference that explains the variability present in the figure.

We have added different symbols per organoid for the interneuron quantifications and moved this quantification to main Figure 2.

(13) I believe it is currently the standard error of the mean which is displayed in the figure, which is not an appropriate representation for variability, or the reproducibility across individual data points. SEM quantifies the reproducibility of the mean, not the reproducibility of the individual data points, which matters here. Mean refers to the mean of this quantification experiment and therefore it's not a biological entity. A box plot showing the interquartile range besides the individual data points would be an accurate representation of the spread of the data.

We agree and have adapted the data, now in Figure 5, accordingly.

(14) Again, in general, the main figures should contain much more of the quantification, as opposed to just raw images.

Quantifications have been added in Figure 2 for the GAD67/NeuN for all cell lines as well as a time course quantification of GAD67/NeuN for 1 of the cell lines. In Figure 4, we have added excitatory and inhibitory synaptic quantifications.

(15) Figure 2F-I the location of the center of the rosette should be marked with a star so that the conclusion about the direction of processes can be established.

The suggested addition of a marker at the center of each rosette was evaluated but not implemented, because it reduced rather than improved figure clarity.

(16) Figure 3 b and c:

High magnification images of single cells, can't show changes in cell type morphology, and one cannot conclude that these cells are present in significant numbers across time. Zoomed-out images or quantification would be necessary for such a claim. The authors already have such images as presented in the next panels, so quantification without new experiments.
> I am uncertain about the T3 supplement here - do these images correspond to the same conditions?

(a) It is unclear to me why different markers are used in the different panels, namely why NG2 is not used in any of the other images.

NG2 was used at early developmental time points to show the presence of Oligodendrocyte Precursor Cells (OPCs). At later time points, the focus switched to MBP staining to indicate more mature oligodendrocyte lineage cells. Although NG2 and MBP are not in the same panels, the staining was performed for both antibodies at the same developmental time point (Day 119) as seen in Figure 3C and 3D.

(b) Color coding in Figure 3G is ambiguous; the use of two blues should be avoided, and the Sub-sub panels should be individually labeled for the color code.

We agree, and have now used different colors.

(c) It is unclear if the presence of the t3 molecule is part of the standard procedure or if it was a side experiment to enhance the survival of oligodendrocytes. Are there no oligodendrocytes without? How does T3 affect other cell types, and the general health and differentiation of the cultures?

Indeed, T3 is essential for oligodendrocyte formation. We did not observe obvious effects on the general health or differentiation potential of the cultures.

(d) Is the 2ng/ml t3 from day one to the final day?

Indeed, in the organoids cultured to study oligodendrocyte formation, T3 was added from Day 1. These details have now been clarified in the Methods and Results sections.

(17) Figure 4:

(a) Microscopy in this figure is high quality and very convincing about neural maturity.

(b) The term "cluster" should be avoided. Unclear what it means here, but my best guess is "cells in a frame of view." Cluster is used with a different meaning in electrophysiology.

This was adapted to ‘neurons in a field of view (FOV)’.

(c) Panel J: I assume each row corresponds to a single cell? Could this be clarified? Are these selected cells from each frame, or all active cells are represented?

Indeed, each row corresponds to a single cell, showing all active cells in the frame. This is now clarified in the legend.

(d) How many Wells do these data correspond to, and in which line it was measured?

As reported in the legend for Figure 5, these data correspond to 2 wells at Day 61 to which we have now added calcium imaging data from 3 wells from a different batch at Day 100. We have included in the legend that these recordings were from Line 1.

(e) Panels G to I, again, the use of standard error of the mean is inappropriate and misleading: looking at the error bar one must conclude that there is minimal variation, which is the exact opposite of the conclusions, when one would look at the variability of the raw data points.

As suggested, the graphs have been adapted as boxplots with interquartile ranges to highlight the distribution of data points.

(f) It is unclear how many neurons and how many total actively firing neurons are present in the videos analyzed

All neurons that were active in the field of view and showed at least one calcium event during the ~10 minute recording were included in the analysis. Using this method, we cannot comment on the proportion of neurons that were active from the total amount of neurons present, since the AAV virus we used does not transduce all neurons.

(g) This figure shows the strength of the method in achieving neural maturity and function. There seems to be that there is considerable activity in the neuronal cultures analyzed. To conclude how reliably the method leads to such mature cultures one would need to measure at least a dozen wells (even if with some simpler and low-resolution method). Concluding reproducibility from one or two hand-picked examples is not possible.

We agree with the reviewer that the number of wells used for calcium imaging analysis was limited. We are currently working on more advanced methods to increase the throughput of this analysis. However, we’ve now added another timepoint to the calcium imaging data in Figure 5 from an independent batch of 3 adherent cortical organoids, which demonstrates continued robust activity at Day 100, as well as Day 61.

Methods:

(1) Stem cell culture. The artist described that line 3 is grown on MEFs. Is this true for the other two lines, furthermore were they cultured in identical conditions?

Line 2 and 3 were not grown on MEFs. We specifically chose different sources of NPCs to reflect the robust nature of the differentiation protocol. We have recently also adapted the protocol from Line 3 NPCs to confirm that the protocol also works starting from hiPSCs grown in feeder-free conditions in StemFlex medium, by adapting NPC differentiation according to our recent publication in Frontiers in Cellular Neuroscience (Eigenhuis et al 2023).

(2) "NPCs were differentiated to adherent cortical organoids between passages 3 and 7 after sorting." Please clarify this sentence. I assume it refers to the first facs sorting of the protocol, but a section is not sufficiently detailed.

We have adapted the methods to clarify that the FACS purification step occurs at the NPC stage.

(3) I didn't fully understand: It seems to be that there are two steps of fact sorting involved, one after passage 3 and one after week 4. This should be represented in the graphical abstract of Figure 1.

As outlined above, there is only 1 FACS sorting step at NPC stage. We have adapted this in the Methods and in the graphical abstract.

(4) Neural differentiation: The authors write that optimal seeding density was determined by visual inspection of the organoids - this is.

We have clarified the Methods section to better explain the process of optimizing the seeding density for each NPC line to generate the ACOs.

(5) What does the following sentence mean: "Cells were refreshed every 2-3 days." Does it mean in replacement of the complete media? How much Media was added to the Wells?

This is a very good point that we have now clarified in the Methods, as full replenishment of media is neither feasible, nor desirable. From the total volume of 110 µl per well, 80 µl is taken out and replaced with 85 µl to compensate for evaporation.

(6) Calcium imaging: can the authors explain the decision to move the cultures one day before imaging into brainphys neural differentiation medium? In 3D organoid protocols, brainphys is gradually introduced to avoid culture shock (very different composition), and used for multiple months to enhance neural differentiation. For recording electrophysiological activity, artificial CSF is the most common choice.

Indeed, for whole cell recordings of 2D neural networks as performed in Günhanlar et al 2018, we used gradual transition to aCSF. For the current ACOs, we found that using BrainPhys from the start of organoid differentiation prevents structure formation, probably because of increased speed of maturation disrupting proliferation and organization of radial glia differentiation. However, by changing the media to BrainPhys just one day before recording (reflecting a gradual change as not all medium is fully replenished and easier than switching to aCSF during recording), we saw greatly improved neuronal activity.

(7) Statistical analysis : As I pointed out before, the standard error of the mean is not an appropriate metric to represent the variability of the data. It is meant to represent the variability of the estimated average. The following thought experiment should make it clear: I measured the expression of a gene in my system. 50 times I measured 0 and 50 times I measured 100. The average is 50, but of course it is a very bad representation of the data because no such data points exist with that value. Yet the standard error of the mean would be plus minus 5.

We have revised Figures 5C–5D to boxplots displaying the interquartile range with all individual data points overlaid, which more accurately represents the variability in the dataset.

Discussion

(1) The discussion focuses on human cortical development, however, the methods presented by the authors entail dissociation and replating through multiple stages not part of brain development. I see the approach as more valuable as a possibly reliable method that generates both diverse and mature neural cultures.

We have revised the Discussion to avoid explicitly invoking an in vitro recapitulation of human cortical development. Nevertheless, given that the NPCs from which the organoids originate exhibit frontal cortical identity, coupled with the timely emergence of cortical neuronal markers and rudimentary cortical layering, we are increasingly confident that the development of these cultures most likely mirrors that of the frontal cortex. To further substantiate this hypothesis, single-cell RNA sequencing experiments will be conducted in the future to provide additional insights.

(2) One of the major claims of the authors is that the method is very reproducible. However, there is almost no data on reproducibility throughout the paper. Mostly single, high magnification images are presented, which therefore represent a small region of a single well of a single batch of a single cell line. Based on the data presented it is not possible to evaluate the reproducibility of the method.

We agree that the original version did not sufficiently document reproducibility. To address this, we have refined and expanded our presentation of reproducibility data. The previous success-rate panel (original Figure S1D) has been moved and adapted as the new Figure S1C. In this updated version, each dot still represents the endpoint success rate of an independent batch, but dot size now scales with batch size (10–40 organoids), and the legend specifies the total numbers of organoids analyzed per line (line 1: n=248; line 2: n=70; line 3: n=70). Together with the distribution of success rates between ~40– 90% across multiple time points and three iPSC lines, this more detailed representation allows readers to directly assess the robustness of line-to-line and batch-to-batch performance. In addition, new time course quantifications of interneuron proportion (Figure 2G,H), synaptic marker densities (Figure 4H, I), and late-stage calcium imaging (Figure 5C,D,E) further demonstrate that key structural and functional read-outs show overlapping ranges across lines and independent differentiations, reinforcing that the method yields reproducible core phenotypes despite some biological variability.

(3) The data presented is very promising, and it suggests that the authors derived optimal conditions for neural differentiation and neural culture diversification. I am confident that the authors can show that reproducibility, at least in a practical sense (e.g. in wells that form a culture) is high.

Overall, this is a very promising and exciting work, that I am looking forward to reading in a mature manuscript.

Reviewer #2 (Recommendations for the authors):

(1) Direct head-to-head comparison with standard organoid culture seems to be missing and may be valuable for benchmarking, ie what can be done with the new method that cannot be done with standard culture and vice versa, ie what are the aspects in which new method could be inferior to the standard.

We have now more clearly elaborated the differences with other methods. As addressed in our response to point 2 of Reviewer 1 in the public reviews, there are several limitations and advantages to the adherent cortical organoids model listed as follows:

Advantages of adherent cortical organoids:

(1) Higher order self-organized structure formation, including segregation of deeper and upper cortical layers.

(2) Longevity: adherent cortical organoids can be successfully kept in culture for at least 1 year, whereas 2D cultures typically deteriorate after 8-12 weeks.

(3) Maturity, including the formation of dendritic mushroom spines and robust electrophysiological activity.

(4) Cell type diversity including a more physiological ratio of inhibitory and excitatory neurons (10% GAD67+/NeuN+ neurons in adherent cortical organoids, vs 1% in 2D neural networks), and the emergence of oligodendrocyte lineage cells.

On the other hand, limitations of adherent cortical organoids compared to 2D neural network cultures include:

(1) Culture times for organoids are much longer than for 2D cultures and the method can therefore be more laborious and more expensive.

(2) Whole cell patch clamping is not easily feasible in adherent cortical organoids because of the restrictive geometry of 384-well plates.

(2) It would be important to further benchmark the throughput, ie what is the success rate in filling and successfully growing the organoids in the entire 384 well plate?

We have addressed this question in the current version of Fig. S1C, in which multiple batches of organoids of all three lines were scored for their success rate. The graph reflects the proportion of properly formed organoids of +/- 400 seeded wells scored at different timepoints, in which each timepoint is a different batch. As mentioned in the response to Reviewer 1, we have also added data on the number of organoids seeded per line in the figure legend.

(3) For each NPC line an optimal seeding density was estimated based on the proliferation rate of that NPC line and via visual observation after 6 weeks of culture. It would be important to delineate this protocol in more robust terms, in order to enable reproducibility with different cell lines and amongst the labs.

As outlined in the response to Reviewer 1, we have clarified the Methods and Discussion sections on seeding density and proliferation rate.

Reviewer #3 (Recommendations for the authors):

Kroeg et al. have introduced a novel method to produce 3D cortical layer formation in hiPSC-derived models, revealing a remarkably consistent topography within compact dimensions. This technique involves seeding frontal cortex-patterned iPSC-derived neural progenitor cells in 384-well plates, triggering the spontaneous assembly of adherent cortical organoids consisting of various neuronal subtypes, astrocytes, and oligodendrocyte lineage cells. Compared to existing brain organoid models, these adherent cortical organoids demonstrate enhanced reproducibility and cell viability during prolonged culture, thereby providing versatile opportunities for high-throughput drug discovery, neurotoxicological screening, and the investigation of brain disorder pathophysiology. This is an important and timely issue that needs to be addressed to improve the current brain organoid systems. While the authors have provided significant data supporting this claim, several aspects necessitate further characterization and clarification. Particularly, highlighting the consistency of differentiation across different cell lines and standardizing functional outputs are crucial elements to emphasize the future broad potential of this new organoid system for large-scale pharmacological screening.

(1) Considering the emergence of astrocyte markers (GFAP, S100b) and upper layer neuron marker (CUX1) around Day 60, the overall differentiation speed is significantly faster compared to other forebrain organoid protocols. Are these accelerated sequences of neurodevelopment consistent across different hiPSC lines?

As shown in Fig. S5, astrocytes are present around Day 60 for all three lines. For comparison with other organoid protocols, an important consideration is that the timeline for these organoids starts at NPC plating, while for other protocols timing often starts from the hiPSC stage. We have clarified the timeline in the graphical abstract in Figure 1A and in the Methods.

(2) The calcium imaging results in Figure 4G were recorded at a single time point, Day 61, a relatively early time window compared to other forebrain organoid protocols (more than 100 days, PMID: 31257131; PMID: 36120104). Are the neurons in adherent cortical organoids functionally mature enough around Day 61? How consistent is this functional activity across different cell lines and independent differentiation batches?

As discussed above in Point 1, it is important to consider that the specified timeline starts from NPC plating. In analogy to 2D neural networks, robust neuronal activity can be observed after ~8 weeks in culture. In addition, we have now added calcium imaging data for an additional batch of organoids at Day 100 in Figure 5, which exhibit comparable levels of neuronal activity as observed on Day 61.

(3) Along the same line, Various cell types, such as oligodendrocytes and astrocytes, are believed to influence neuronal maturation. Therefore, longitudinal studies until the late stage are necessary to observe changes in electrophysiological activity based on the degree of neuronal maturation (at least two more later time points, such as 100 days and 150 days).

As described in the previous points, we have now included a Day 100 time point in the calcium imaging data, in addition to the recordings at Day 61 (Figure 5C-E).

(4) The authors assert that heterogeneity among organoids has been diminished using the human adherent cortical organoids protocol. However, there is inadequate quantitative data to prove the consistency of neuronal activities between different wells. Therefore, experiments quantifying the degree of heterogeneity between organoids, such as through methods like calcium imaging, are necessary to determine if neuron activity occurs consistently across each organoid well.

We agree with the review and have added several quantitative experiments: a) we’ve added another timepoint to the calcium imaging data in Figure 5 from an independent batch of 3 adherent cortical organoids, which demonstrates continued robust activity at day 100, as well as day 61; b) we added synapse quantification in Figure 4, and c) interneuron quantification in Figure 2. We are currently also pursuing high throughput measures of activity to assess the longitudinal activity of ACOs in a larger number of wells. This way we can more definitively quantify the time-dependent variance in organoid activity.

(5) Is this platform applicable to other functional measurements for neuronal activity, such as the MEA system? When observing the morphology of neurons formed in organoids, they appear to extend axons and dendrites in a consistent direction, suggesting a radial structure that demonstrates high reproducibility across wells. A culture system where neurons are arranged with such consistency in directionality could be highly beneficial for experiments utilizing the MEA system to assess parameters such as the speed of electrical activity transmission and stimulus-response. Therefore, there seems to be a need for a more detailed explanation of the utility of the structural characteristics of the culture system.

The ACO platform is indeed suitable for MEA recordings. We are in the process of engineering the required geometry using HD-MEA systems through specialized inserts to generate ACOs on MEA systems.

(6) In Figure 2E-I, authors suggest morphological diversity of GFAP+/S100b+ astrocyte, but the imaging data presented in Figure F-I is only based on GFAP immunoreactivity.

Since GFAP is also expressed in radial glial cells at this stage (Figure 2I), many fibrous astrocytes and interlaminar astrocytes are likely radial glial neural progenitor cells instead of astrocytes. It appears necessary to perform additional staining using astrocyte markers such as S100B or outer radial glia markers such as HOPX to demonstrate that the figure depicts subtype-specific morphologies of astrocytes.

In Figure 2M, we stained for GFAP and PAX6 to mark radial glia that look different than the astrocyte morphologies we describe in Figure 2J-L. We see a large overlap in GFAP and S100B staining in Figure 2I, in which most GFAP+ cells are double positive for S100B (yellow) that is more consistent with astrocyte maturation than radial glia. Furthermore, we have not seen PAX6 staining outside the dense edges of the center of the ACO.

(7) In Figure 4D, the axon appears to exhibit directionality. Additional explanation regarding the organization of the axon is necessary. Further research utilizing sparse staining to examine the morphology of single neurons seems warranted.

The polarized directionality of the axons is something we indeed have also noticed. We are looking into options to further investigate this intriguing property of the ACOs.

(8) Figure 1E-F only showed cell viability in the early stages around Day 40-50. To demonstrate the superior long-term viability of ACO culture, it appears necessary to illustrate the ratio of dead cells to live cells over the course of a time course.

Figure S1B shows LIVE/DEAD staining for ACOs of all three lines, revealing minimal DEAD staining at Day 56. A longitudinal time course experiment was not performed, however the line- and batch-specific quantifications over developmental timepoints in Figure S1C provide an indication of the robust long-term viability of the ACOs.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this fMRI study, the authors wished to assess neural mechanisms supporting flexible temporal construals. For this, human participants learned a story consisting of fifteen events. During fMRI, events were shown to them, and participants were instructed to consider the event from "an internal" or from "an external" perspective. The authors found distinct patterns of brain activity in the posterior parietal cortex (PPC) and anterior hippocampus for the internal and the external viewpoint. Specifically, activation in the posterior parietal cortex positively correlated with distance during the external-perspective task, but negatively during the internal-perspective task. The anterior hippocampus positively correlated with distance in both perspectives. The authors conclude that allocentric sequences are stored in the hippocampus, whereas egocentric sequences are supported by the parietal cortex.

We thank the reviewer for the accurate summary of our study.

Strengths:

The research topic is fascinating, and very few labs in the world are asking the question of how time is represented in the human brain. Working hypotheses have been recently formulated, and the work tackles them from the perspective of construals theory.

We appreciate the reviewer's positive and encouraging comments.

Weaknesses:

Although the work uses two distinct psychological tasks, the authors do not elaborate on the cognitive operationalization the tasks entail, nor the implication of the task design for the observed neural activation.

We thank the reviewer for bringing this issue to our attention. In the revised manuscript, we have added a paragraph to the Discussion acknowledging this potential limitation of the study. Please see our response below.

Reviewer #1 (Recommendations for the authors):

Overall, I thank the authors for providing clear responses and much-needed detail on their original work, which enables a better understanding of their perspectives. I still have some detailed questions about the reported work, which I provide below. It could help clarify the work for a more general audience and its replicability by the community.

We thank the reviewer for their positive evaluation of our previous revisions.

Main general concern:

I have one remaining core concern, which I distill as being a very different take on the usefulness of task design with neuroimaging. This concern follows from the authors' response to my original comment, which suggested possible confounds in fMRI data analysis and interpretation, as differences in task design and behavioral outcomes were not incorporated in the analytical approach.

The authors confirmed that "there is a substantial difference between the two tasks" but argue that these differences are not relevant seing that "the primary goal of this study was not to directly compare these tasks to isolate a specific cognitive component " However, the authors do perform such contrasts in their analysis (e.g. p. 10: "We first directly contrasted the activity level between external- and internal-perspective tasks in the time window of...") and build inferences on brain activation from them (e.g., p. 10: "Compared with the internal-perspective task, the externalperspective task specifically activated the...").

To clarify, my original concern was not about comparing neural activity in response to the two tasks but about the brain activity generated by two distinct tasks, which aim to reveal fundamentally distinct neural processes. The authors' response raises several concerns about the theoretical, methodological and empirical foundation of the work that are beyond the scope of a single empirical study and too long to detail here. Cognitive neuroscience relies on tasks to infer neural processes; this is the fertile and essential ground for using behavior in neuroscience to get to a mechanistic understanding of brain functions (e.g., Krakauer et al., 2017). In short, task design is fundamental because it shapes what neural processes are being investigated. Any inferences about brain activity recorded while a participant performs a task result from manipulated variables that should be under the control of the experimenter. Acknowledging that two tasks are distinct is acknowledging that different (neural) processes may govern their resolution. My initial remark was meant to highlight that, from basic signal detection theory, a same/different task and a temporal order task may not yield the same kind of basic biases and decision-making processes; these are far below and more basic than the posited sophisticated representations herein (construals, perspective taking).

In short, the general approach is far coarser than the level of interpretational granularity being pushed forward in the paper would suggest.

We greatly appreciate the reviewer’s comments and agree that this is a very fair point. We acknowledge that the two tasks differ in their underlying decision-making processes. In the revised manuscript, we have added a paragraph at the end of the Discussion to explicitly acknowledge this limitation and to outline possible avenues for future research (Page 23).

“One limitation of the present study is that the external- and internal-perspective tasks differed not only in the type of perspective-taking they were intended to elicit, but also in their underlying decision-making processes. The external-perspective task explicitly required participants to compare two events with respect to external temporal landmarks and judge whether they occurred in the same or different parts of the day (i.e., a same/different judgment), whereas the internalperspective task explicitly required participants to project themselves into a reference event and judge whether the target event occurred in the future or the past relative to that reference (i.e., a temporal-order judgment). This task design ensured that participants adopted two distinct perspectives on the event series, but at the expense of coherence in the cognitive operations required to make the two types of judgments. One alternative approach would be to more closely align the response demands of the two tasks by drawing on McTaggart’s (1908) A-series and Bseries distinction: in the external-perspective task, participants could judge whether the target event occurred before or after the reference event (i.e., a before/after judgment), whereas in the internal-perspective task they could judge whether the target event occurred in the past or future relative to the reference event (i.e., a past/future judgment). Although such a design would improve coherence in the underlying decision-making processes (i.e., both are temporal-order judgments), it would reduce experimental control over the perspective-taking manipulation. For example, before/after judgments could still be made from an internal perspective. Future studies are therefore needed to determine whether findings obtained from these two task designs converge.”

Additional clarifications:

Intro/theory

In this revised MS, the authors provided some clarifications of their theoretical perspective in the introduction. From my standpoint, the motivation remains insufficiently precise for a scientific report. Some theoretical aspects, such as construals or perspective taking remain evasive in relation to ego and allocentric representations. A couple of paragraphs dedicated to explaining what the authors mean precisely when using these terms would greatly help to situate the validity of the working hypothesis. In the absence of clear definitions, it remains difficult to evaluate what is being tested. For instance, what do the authors mean by "time construal"? How is a time construal the same or not as a "temporal distance" or a "temporal sequence"? This would greatly help the readership.

Additionally, some assertions are not clearly identified or fairly attributed. For instance, the assertion that EST provides a means to spatialize time is the authors' point of view or interpretation of this work, not an original proposition of the theory. Another example is McTaggart's metaphysics on time series (in the ontology of time in physics) "echoed" in linguistics; it has effectively been proposed and popularized by L. Boroditskty. The prospective and retrospective views of time should not be attributed to Tsao et al but to Hicks or Block in the 70's, who studied the psychology of time in humans.

We sincerely thank the reviewer for this criticism, which prompted us to clarify the relevant concepts in our manuscript. In the revised version, we made the following three main changes to the Introduction.

In the second paragraph of the Introduction (page 3), we clarify that event segmentation theory is independent of, but related to, the spatial construal of time hypothesis. We also clarify what we mean by time construals and explain that the two temporal components—duration and sequence—can be represented within such time construals, rather than constituting time construals themselves. These revisions were intended to prevent potential misunderstandings for the reader. In addition, we incorporated Boroditsky’s contributions relevant to this framework:

“One solution, which might be unique to humans, is to conceptualize time in terms of space (i.e., the spatial construal of time; e.g., Clark, 1973; Traugott, 1978; Lakoff & Johnson, 1980). Within this framework, time is usually first segmented into events—the basic temporal entities that observers conceive as having a beginning and an end (Zacks & Tversky, 2001). These temporal entities are then ordered in space, such that events occurring at different times can be maintained in working memory, allowing them to be flexibly accessed from different perspectives and easily referenced during communication (e.g., Casasanto & Boroditsky, 2008; Núñez & Cooperrider, 2013; Bender & Beller, 2014; Abrahamse et al., 2014; Figure 1A). The two core temporal components—duration and sequence—can be readily represented in such time construals.”

In the third paragraph of the Introduction (pages 3-4), we acknowledge the contributions of earlier behavioral studies on prospective and retrospective timing by citing the work suggested by the reviewer (Block & Zakay, 1997), which indicates that two distinct cognitive systems underlie timing processes. These behavioral findings converge with the conclusions of more recent neuroimaging studies:

“Unlike prospective timing tracking the continuous passage of time, durations in time construals are event-based (Sinha & Gärdenfors, 2014): the interval boundaries are constituted by events, and the event durations reflect their span (Figure 1A). Accumulating evidence suggests that distinct cognitive systems underlie these two types of duration (e.g., Block & Zakay, 1997). The motor and attentional system—particularly the supplementary motor area—has been associated with prospective timing (e.g., Protopapa et al., 2019; Nani et al., 2019; De Kock et al., 2021; Robbe, 2023), whereas the episodic memory system—particularly the hippocampus—is considered to support the representation of duration embedded within an event sequence (e.g., Barnett et al., 2014; Thavabalasingam et al., 2018; see also the comprehensive review by Lee et al., 2020).”

Block, R. A., & Zakay, D. (1997). Prospective and retrospective duration judgments: A meta-analytic review. Psychonomic Bulletin & Review, 4(2), 184-197.

In the fifth paragraph of the Introduction (page 5), we added a sentence to clarify the relationship between allocentric and egocentric reference frames and perspective taking:

“However, the neural mechanisms that enable the brain to generate distinct construals of an event sequence remain largely unknown. Valuable insights may be drawn from research in the spatial domain, which posits the existence of stable allocentric representations that are independent of viewpoint, from which variable egocentric representations corresponding to different perspectives can be generated.”

Methods:

While more detail is provided in the Methods, some additional detail would be helpful to enable the replication of this work. For instance,

- The table reports a sequence of phrases with assigned durations. Are the event phrases actual sentences given to participants? If so, how were participants made aware of the duration of the events, seeing that these sentence parts do not provide time information?

We apologize that we did not make this clear. The full text used during the reading phase of learning has already been provided in Figure 1—source data 1, which includes the information about event durations. In the revised manuscript, we now explicitly refer to this information in the Methods section (page 38): In the reading phase, participants read a narrative describing the whole ritual on a computer screen twice (Figure 1—source data 1).

- One of my original questions was about the narrative. In the Methods section, the authors state that participants read a text. Providing the full text would be helpful, also as a sanity check for sequentiality.

As clarified in the previous response, the texts are provided in Figure 1—source data 1, which illustrates the texts for both even- and odd-numbered participants.

- In the imagination phase, the authors introduce proportionality between imagination and experience (p. 37). What scale was used? What motivated it?

We thank the reviewer for bringing this issue to our attention. In this study, participants did not directly experience the events; instead, they learned the event information through narrative reading or imagination to ensure experimental control and efficiency. As clarified in the Methods section, the ratio between imagination duration and actual event duration was 30 seconds to 1 hour. In the revised manuscript, we have further explained our motivation for this design choice (page 39):

Here, we let participants learn the event information through narrative reading or imagination. Compared to learning through actual experience, this approach prioritizes experimental control and efficiency. The timing of the events is compressed, akin to the process of retrospectively recalling our experiences, in which we mentally traverse events without requiring the actual time they originally took. However, future studies may be needed to investigate whether the encoding of events from first- and second-hand experience differs.

Results:

- p. 10: the interpretation of the data on chunking and boundary effects should be properly referenced to e.g. Davachi's published work.

We thank the reviewer for highlighting Davachi’s important work on event boundaries. We have appropriately cited these studies in the revised manuscript (page 10), as reflected in the following passage: This pattern can be interpreted as a categorical effect: sequential distances within the same part of the day were perceived as shorter (i.e., a chunking effect), whereas distances spanning different parts of the day were perceived as longer (i.e., a boundary effect). Similar boundary- or chunking-related effects on event cognition have been reported in previous studies (e.g., Ezzyat & Davachi, 2011; DuBrow & Davachi, 2013; Radvansky & Zacks, 2017).

Ezzyat, Y., & Davachi, L. (2011). What constitutes an episode in episodic memory?. Psychological Science, 22(2), 243-252.

DuBrow, S., & Davachi, L. (2013). The influence of context boundaries on memory for the sequential order of events. Journal of Experimental Psychology: General, 142(4), 1277.

Radvansky, G. A., & Zacks, J. M. (2017). Event boundaries in memory and cognition. Current Opinion in Behavioral Sciences, 17, 133-140.

Reviewer #2 (Public review):

Summary:

Xu et al. used fMRI to examine the neural correlates associated with retrieving temporal information from an external compared to internal perspective ('mental time watching' vs. 'mental time travel'). Participants first learned a fictional religious ritual composed of 15 sequential events of varying durations. They were then scanned while they either (1) judged whether a target event happened in the same part of the day as a reference event (external condition); or (2) imagined themselves carrying out the reference event and judged whether the target event occurred in the past or will occur in the future (internal condition). Behavioural data suggested that the perspective manipulation was successful: RT was positively correlated with sequential distance in the external perspective task, while a negative correlation was observed between RT and sequential distance for the internal perspective task. Neurally, the two tasks activated different regions, with the external task associated with greater activity in the supplementary motor area and supramarginal gyrus, and the internal condition with greater activity in default mode network regions. Of particular interest, only a cluster in the posterior parietal cortex demonstrated a significant interaction between perspective and sequential distance, with increased activity in this region for longer sequential distances in the external task but increased activity for shorter sequential distances in the internal task. Only a main effect of sequential distance was observed in the hippocampus head, with activity being positively correlated with sequential distance in both tasks. No regions exhibited a significant interaction between perspective and duration, although there was a main effect of duration in the hippocampus body with greater activity for longer durations, which appeared to be driven by the internal perspective condition. On the basis of these findings, the authors suggest that the hippocampus may represent event sequences allocentrically, whereas the posterior parietal cortex may process event sequences egocentrically.

We sincerely appreciate the reviewers for providing an accurate, comprehensive, and objective summary of our study.

Strengths:

The topic of egocentric vs. allocentric processing has been relatively under-investigated with respect to time, having traditionally been studied in the domain of space. As such, the current study is timely and has the potential to be important for our understanding of how time is represented in the brain in the service of memory. The study is well thought out and the behavioural paradigm is, in my opinion, a creative approach to tackling the authors' research question. A particular strength is the implementation of an imagination phase for the participants while learning the fictional religious ritual. This moves the paradigm beyond semantic/schema learning and is probably the best approach besides asking the participants to arduously enact and learn the different events with their exact timings in person. Importantly, the behavioural data point towards successful manipulation of internal vs. external perspective in participants, which is critical for the interpretation of the fMRI data. The use of syllable length as a sanity check for RT analyses as well as neuroimaging analyses is also much appreciated.

We thank the reviewer for the positive and encouraging comments.

Suggestions:

The authors have done a commendable job addressing my previous comments. In particular, the additional analyses elucidating the potential contribution of boundary effects to the behavioural data, the impact of incorporating RT into the fMRI GLMs, and the differential contributions of RT and sequential distance to neural activity (i.e., in PPC) are valuable and strengthen the authors' interpretation of their findings.

My one remaining suggestion pertains to the potential contribution of boundary effects. While the new analyses suggest that the RT findings are driven by sequential distance and duration independent of a boundary effect (i.e., Same vs. Different factor), I'm wondering whether the same applies to the neural findings? In other words, have the authors run a GLM in which the Same vs. Different factor is incorporated alongside distance and duration?

We thank the reviewer for their positive evaluation of our previous revisions and are pleased that the additional analyses adequately address the boundary effects in the behavioral data and the RT effects in the neural data.

With respect to boundary effects in the neural data, we followed the reviewer’s suggestion and constructed a more complex GLM that incorporated the Same/Different part of the day as an additional regressors modulating the target events. Importantly, the same PPC region continued to show an interaction effect between Task Type and Sequential Distance. We have added this important control analysis in our revised manuscript (Pages 13–14):

“To further assess whether the observed PPC reactivation can be attributed to boundary or chunking effects introduced by the Parts of the Day, as well as other behavioral outputs, we performed an additional control analysis. Using a more complex first-level model, we included two extra regressors modulating the target events in both internal- and external-perspective tasks, alongside Sequential Distance and Duration: (1) Same/Different parts of the day (coded as 1/−1) and (2) Future/Past (coded as 1/−1). Even with these additional controls, the same PPC region remained the strongest area across the entire brain, showing an interaction effect between Task Type and Sequential Distance, although the cluster size was slightly reduced (voxel-level p < 0.001; clusterlevel FWE-corrected p = 0.054).”

Author response:

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

We thank the reviewers for their enthusiasm and insightful suggestions. Our responses to specific concerns and questions are detailed below.

Public Reviews:

Reviewer #1 (Public review):

The authors use Flow cytometry and scRNA seq to identify and characterize the defect in gdT17 cell development from HEB f/f, Vav-icre (HEB cKO), and Id3 germline-deficient mice. HEB cKO mice showed defects in the gdT17 program at an early stage, and failed to properly upregulate expression of Id3 along with other genes downstream of TCR signaling. Id3KO mice showed a later defect in maturation. The results together indicate HEB and Id3 act sequentially during gdT17 development. The authors further showed that HEB and TCR signaling synergize to upregulate Id3 expression in the Scid-adh DN3-like T cell line. Analysis of previously published Chi-seq data revealed binding of HEB (and Egr2) at overlapping regulatory regions near Id3 in DN3 cells.

The study provides insight into mechanisms by which HEB and Id3 act to mediate gdT17 specification and maturation. The work is well performed and clearly presented. We only have minor comments.

Reviewer #2 (Public review):

Summary:

The manuscript by Selvaratnam et al. defines how the transcription factor HEB integrates with TCR signaling to regulate Id3 expression in the context of gdT17 maturation in the fetal thymus. Using conditional HEB ablation driven by Vav Cre, flow cytometry, scRNA-seq, and reanalysis of ChIP-seq data the authors, provide evidence for a sequential model in which HEB and TCR-induced Egr2 cooperatively upregulate Id3, enabling gdT17 maturation and limiting diversion to the ab lineages. The work provides an important mechanistic insight into how the E/ID-protein axis coordinates gd T cell specification and effector maturation.

Strengths include:

(1) The proposed model that HEB primes, TCR induces, and Id3 stabilizes gdT17 cells in embryonal development is elegant and consistent with the findings.

(2) The choice of animal models and the study of a precise developmental window.

(3) The cross-validation of flow, scRNA-seq, and ChIP-seq reanalyses strengthens the conclusions.

(4) The study clarifies the dual role of Id3, first as an HEB-dependent maturation factor for gdT17 cells, and as a suppressor of diversion to the ab lineages.

Weaknesses:

(1) The ChIP-seq reanalysis indicates overlapping HEB, E2A, and Egr2 peaks ~60 kb upstream of Id3. Given that the Egr2 data are not generated using the same thymocyte subsets, some form of validation should be considered for the co-binding of HEB and Egr2, potentially ChIP-qPCR in sorted gdT17 progenitors.

We agree that this is a valid concern and continue to work on confirming the mechanism from several other angles. Validating HEB/E2A and Egr2 co-binding in gdT17 cell progenitors by ChIP-qPCR would/will be a very precise and definitive experiment, but it will be very challenging to perform, in part due to the low numbers of gdT17 precursors in the fetal thymus (note the y-axis scales in Fig. 1F, J). As a complementary approach, we have analyzed additional ChIP-seq data for HEB/E2A binding in Rag2^-/- DN3 cells retrovirally transduced with the KN6 gdTCR cultured with stroma expressing the weak KN6 ligand T10 for 4 days. This analysis revealed that the binding of HEB/E2A on those sites persisted after weak gdTCR signaling, strengthening the likelihood that concurrent binding of HEB/E2A and Egr2 occurs during this developmental transition. We noted that HEB/E2A binding was slightly dampened in Rag2^-/- DN3 + gdTCR cells relative to Rag2^-/- DN3 cells, consistent with the induction of Id3 and subsequent Id3-mediated disruption of E protein binding. We also located HEB/E2A and Egr binding sites in close proximity in the two regions that shared peaks between HEB/E2A and Egr2 analyses (HE1 and HE2), in line with the potential participation of these two transcription factors in an enhanceosome binding complex.

Furthermore, we examined the chromatin landscape of the Id3 locus by sorting WT DN3 and DN4 cells, as well as Rag2^-/- DN3 cells to provide a genuine pre-selection context, and performing ATAC-seq (Figure 7–suppl 7A). Given the known ability of E2A and HEB to induce chromatin remodeling, we also examined accessibility in DN3 and DN4 cells from HEB cKO mice. Alignment of ATAC-seq and ChIP-seq peaks in the Id3 locus revealed accessibility of HE1 and HE2 in Rag2^-/-, WT DN3, and WT DN4 cells. However, accessibility of HE1 and HE2 was dampened in HEB cKO cells, especially at the DN3 stage, suggesting that HEB may be involved in remodeling the Id3 locus, resulting in a poised state that enables TCR-dependent transcription factors to induce Id3 proportionally to TCR signal strength. These data are now presented as a new “Figure 7 – figure supplement 1” with corresponding Results, Discussion, and Methods updates.

Our next story will be focused on a finer dissection of the Id3 cis-regulatory elements and their combinatorial regulation by HEB/E2A and other transcription factors, and how they relate to specific signaling pathways. For this study, we will modify the language regarding Egr2 to reflect the open questions that still remain to be addressed.

(2) E2A expression is not affected in HEB-deficient cells, raising the question of partial compensation, a point that should be specifically discussed.

This confounding factor is always an issue with E proteins. We have now added a section to the discussion that highlights previous literature and relates it to our findings.

(3) All experiments are done at E18, when fetal gdT17 development predominates. The discussion could address whether these mechanisms extend to neonatal or adult gdT17 subsets.

In our 2017 paper (PMID 29222418) we showed that HEB cKO mice have defects in the production of functional gdT17 cells in fetal and neonatal thymus and in the adult periphery (in lungs and spleen). While the adult thymus does not support the development of fully functional innate gd T cells, it does contain gdTCR+ cells that have activated the Sox-Maf-Rorc network (Yang 2023, PMID 37815917). It will be very interesting to assess the impact of HEB loss on these cells, and we are actively pursuing this goal. For now, we will add a paragraph to the discussion addressing what we know from previous work and what is yet to be learned.

Reviewer #3 (Public review):

Summary:

The authors of this manuscript have addressed a key concept in T cell development: how early thymus gd T cell subsets are specified and the elements that govern gd T17 versus other gd T cell subsets or ab T cell subsets are specified. They show that the transcriptional regulator HEB/Tcf12 plays a critical role in specifying the gd T17 lineage and, intriguingly, that it upregulates the inhibitor Id3, which is later required for further gd T17 maturation.

Strengths:

The conclusions drawn by the authors are amply supported by a detailed analysis of various stages of T cell maturation in WT and KO mouse strains at the single cell level, both phenotypically, by flow cytometry for various diagnostic surface markers, and transcriptionally, by single cell sequencing. Their conclusions are balanced and well supported by the data and citations of previous literature.

Weaknesses:

I actually found this work to be quite comprehensive. I have a few suggestions for additional analyses the authors could explore that are unrelated to the predominant conclusions of the manuscript, but I failed to find major flaws in the current work.

I note that HEB is expressed in many hematopoietic lineages from the earliest progenitors and throughout T cell development. It is also noteworthy that abortive gamma and delta TCR rearrangements have been observed in early NK cells and ILCs, suggesting that, particularly in early thymic development, specification of these lineages may have lower fidelity. It might prove interesting to see whether their single-cell sequencing or flow data reveal changes in the frequency of these other T-cell-related lineages. Is it possible that HEB is playing a role not only in the fidelity of gdT17 cell specification, but also perhaps in the separation of T cells from NK cells and ILCs or the frequency of DN1, DN2, and DN3 cells? Perhaps their single-cell sequencing data or flow analyses could examine the frequency of these cells? That minor caveat aside, I find this to be an extremely exciting body of work.

Excellent question, and the underlying answer is yes, loss of HEB renders the cells more open to divergence to non-T lineages, even at the DN3 stage. Although our datasets did not reveal those cells, we have examined this question previously. In our 2011 paper (Braunstein, 2011, PMID 21189289) where we identified “DN1-like” cells arising from HEB-/- DN3 cells in OP9-DL1 co-cultures. These cells responded to IL-15 and IL-7 by differentiating into cytotoxic NK-like cells. We did not detect TCRb rearrangements but did not look for gdTCR rearrangements. Subsequently, multiple papers from other labs showed that ILC2 were greatly expanded in the thymus using Id-overexpression transgenic mice and HEB/E2A-double deficient mice (Miyazaki, 2023, PMID 28514688; Miyazaki, 2025, PMID 39904558; Berrett, 2019, PMID 31852728; Qian, 2019, PMID 30898894; Peng, 2020, PMID:32817168). The ILCs in these mice had TCRg rearrangements, consistent with a shared origin with WT thymic-derived ILCs. In unpublished data from our lab, we found an increase in the numbers of ILC2 but not ILC3 in HEB cKO fetal thymic organ cultures. We did not follow up on this work any further since the topic was being heavily pursued in other labs, but remain very interested in this branchpoint, and will mention the literature in the discussion.

Joint recommendations for the authors:

(1) Experimental validation (for mechanistic clarity)

The ChIP-seq reanalysis indicates overlapping HEB, E2A, and Egr2 peaks ~60 kb upstream of Id3. Given that the Egr2 data are not generated using the same thymocyte subsets, some form of validation should be considered for the co-binding of HEB and Egr2, potentially ChIP-qPCR in sorted gdT17 progenitors to substantiate the proposed cooperative mechanism.

See above; new experiments with ATAC-seq and additional ChIP-seq analysis.

(2) Figures

Potential inconsistencies in Figure 1H: In the legend to Figure 1H, Vg1-Vg5- cells are considered Vg6+ cells. Flow plots show reduced A Vg1-Vg5- population in HEBc ko mice, but the accompanying bar plot shows increased frequency of Vg6+ cells.

Vg6 cells are actually considered to be Vg4-Vg5-Vg1- cells (not Vg4- Vg1- cells, which is important in the fetal context). The flow plot shows the percentage of Vg6 cells out of the Vg1-Vg4- population, whereas the bar plot shows the percentage of Vg6 cells out of all gdTCR+ cells. The ratio of Vg6 to Vg5 cells decreases within the Vg1-Vg4- population, whereas the overall percentages and numbers of Vg6 cells in all gd T cells is increased in HEB cKO mice. We have now more clearly explained this in the text and the figure legend.

Clarify which cells produce IL-17A in Figure 1L.

This plot is gated on all gd T cells stimulated with PMA/ionomycin; this has been added to the results and figure legend.

In Supplementary Figure 2, legend, do the authors mean that TRGV4 was depleted? The authors write TRDV4. Please check.

Thank you for catching this mistake, we have corrected it.

In Figure 7, the Author showed Id3 mRNA expression. Can the expression of Id2 be included?

That is a really interesting question, and we will follow up on it in future studies.

If Id1 or Id4 are relevant for any of these studies, can their expression be shown in Supplementary Figure 3A? If these are minimally expressed or not expressed, this could be mentioned.

Id1 and Id4 were not detectable in our studies, this is now stated in the results section describing expression of E proteins and Id proteins.

(3) Discussion

Discuss possible redundancy between HEB and E2A, as E2A expression appears unaffected in HEB-deficient cells.

See above

Address whether the mechanisms identified at E18 (embryonic stage) also apply to neonatal or adult γδT17 subsets.

See above

Expand on how HEB function may relate to other hematopoietic or early lymphoid lineages (NK/ILC, DN1-DN3 stages), based on reviewer curiosity.

See above

(4) Methods and terminology

Define the terms γδTe1 and γδTe2 (e.g., early effector subsets).

This has been defined more clearly in several sections of the text.

Add details to the scRNA-seq methods section (average number of cells analyzed and sequencing depth per cell).

These details have been added.

Author response:

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

We now performed new experiments that were included in the manuscript. Our new results show that that monocyte-derived dendritic cells primed in vivo during P. chabaudi infection, or in vitro with TNF express high levels or GLUT-1 (Figures 4M, 5D, 6L). Furthermore, our new data show that mice treated with 2-DG (na inhibitor of glycolysis) are more susceptible to infection (Figures 6N, O). In addition, new results of glucose uptake by muscle and adipose tissues were added to the manuscript. Finally, figure legends were revised, densitometric analysis performed, and other issues addressed in the text.

Please see below a point-by-point reply to the Reviewers’ comments.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The manuscript by Kely C. Matteucci et al. titled "Reprogramming of host energy metabolism mediated by the TNF-iNOS-HIF-1α axis plays a key role in host resistance to Plasmodium infection" describes that TNF induces HIF-1α stabilization that increases GLUT1 expression as well as glycolytic metabolism in monocytic and splenic CD11b+ cells in P. chabaudi infected mice. Also, TNF signaling plays a crucial role in host energy metabolism, controlling parasitemia, and regulating the clinical symptoms in experimental malaria.

This paper involves an incredible amount of work, and the authors have done an exciting study addressing the TNF-iNOS-HIF-1α axis as a critical role in host immune defense during Plasmodium infection.

Reviewer #2 (Public Review):

Summary:

The premise of the manuscript by Matteucci et al. is interesting and elaborates on a mechanism via which TNFa regulates monocyte activation and metabolism to promote murine survival during Plasmodium infection. The authors show that TNF signaling (via an unknown mechanism) induces nitrite synthesis, which (via yet an unknown mechanism), and stabilizes the transcription factor HIF1a. Furthermore, HIF1a (via an unknown mechanism) increases GLUT1 expression and increases glycolysis in monocytes. The authors demonstrate that this metabolic rewiring towards increased glycolysis in a subset of monocytes is necessary for monocyte activation including cytokine secretion, and parasite control.

Strengths:

The authors provide elegant in vivo experiments to characterize metabolic consequences of Plasmodium infection, and isolate cell populations whose metabolic state is regulated downstream of TNFa. Furthermore, the authors tie together several interesting observations to propose an interesting model.

Weaknesses:

The main conclusion of this work - that "Reprogramming of host energy metabolism mediated by the TNF-iNOS-HIF1a axis plays a key role in host resistance to Plasmodium infection" is unsubstantiated. The authors show that TNFa induces GLUT1 in monocytes, but never show a direct role for GLUT1 or glucose uptake in monocytes in host resistance to infection (nor the hypoglycemia phenotype they describe).

We kindly disagree with the Reviewer. There is a series of experiments showing that TNFR KO (Figures 1, 2, 4), HIF1a KO (Figure 5) and iNOS KO (Figure 6) mice have partially impaired inflammatory response and control of parasitemia (Figures Figures 1E, 5G and 6B).

To further address the issue raised by the reviewer, we performed two sets of experiments. First, we show, in vitro, the impact of TNF stimulation on GLUT1 expression and glucose uptake (Figure 4M, 5D, 6L). Our results show that GLUT1 is increased after 18 hours with TNF (100 ng/mL) stimulation in MODCs from WT mice but not from iNOS KO, HIF1a KO e TNFR KO mice. Similar results were obtained with monocytic cells derived from infected mice (Figure 4L, 5C, 6K). The results support the discussion by demonstrating that TNF stimulation influences GLUT1 expression in monocytic cells. This aligns with the proposed mechanism that TNF signaling regulates HIF-1α stabilization and glycolytic metabolism via RNI. The absence of GLUT1 upregulation and glucose uptake in TNFR KO, iNOS KO and HIF-1α KO mice further reinforces the role of RNI in promoting HIF-1α stabilization, as suggested in the discussion.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Major points

All Figure legends are not precise about the data express means {plus minus} standard errors of the means (SEM) or SD. Figure 1D shows no SD in the data from the uninfected group. It strongly suggests precise and improving all figure legends, giving more details in terms of including an explanation of all symbols, non-standard abbreviations, error bars (standard deviation or standard error), experimental and biological replicates, and the number of animals, and representative of the independent experiments.

We apologize for the lack of details in the Figure legends. As requested, we are now indicating whether we used SEM or STDV, number of mice per group, number of replicate experiments. We also clarified the groups that are being compared, and the statistical significance indicated by the symbols. We also standardized symbols as asterisk only, and number of asterisk indicating the significance.

Figure 1. The figure legend has no information about the organ for which TNF mRNA was measured (Figure 1D). Also, regarding the TNF data, Figure 1 C e 1D shows that the circulating levels of TNF and the expression of TNF mRNA in the liver peaked at the same time point, and after 6h, there is no difference between infected and uninfected mice. It would be expected that the TNF mRNA expression would be detected earlier than the protein, assuming that the primary source of TNF is from the liver. Is there another organ that could mainly source blood TNF levels? Did the authors have a chance to measure the blood TNF levels during infection (0-8dpi), besides the measurement at different times only on day 8?

We included in the legend of Figure 1D that mRNA was extracted from liver.

Liver and spleen are the main reservoir of infected erythrocytes and the main source of cytokines during the infection with the erythrocytic stage of malaria. The results presented in Figures 1C and 1D are from in vivo experiments, not a controlled cellular experiment in vitro. So, we can not conclude about exact time and synchronous production of TNF mRNA and protein. We have published earlier that during P. chabaudi infection, the peaks of TNF mRNA expression and the levels of circulating TNF protein occur between midnight and 6 am (Hirako at al., 2018). Hence the results are consistent in the results described here. In addition, this earlier study also shows that the same pattern of TNF at days 6 and 8 post-infection are similar. Furthermore, in another studies, we reported that the peak of TNF production occurs between days 6 and 10 post P. chabaudi infection (Franklin et al, PNAS, 2009; Franklin et al, Microbes and Infection, 2007). This is now clarified in the text (page 05, line 132):

“As previously demonstrated, the circulating levels of TNF and expression of TNF mRNA in the liver peaked at 6 am (end of dark cycle) at 8 dpi (Figure 1C and 1D), and has been reported to peak between days 6 and 10 post-infection, with a consistent pattern observed on days 6 and 8.”

Figure 2. "We observed that in naïve animals, all of these parameters were similar in TNFR^-/- and C57BL/6 mice (Figures 2A-D, top panels, and Figures 2E-H)." Interestingly, the respiratory exchange rate of TNFR^-/- uninfected mice seems higher in TNFR^-/- uninfected mice than in naïve uninfected mice, and this pattern seems to be more pronounced in TNFR^-/- uninfected mice. Is there any suggestion that could explain the change in respiratory exchange rate behavior without infection in those animals?

At the moment, we have not investigated the basis of this difference between uninfected WT and TNFR KO mice, which goes beyond the scope of this research. This is indeed an interesting observation that should be pursued in the future by our group and elsewhere. We mentioned this difference, when describing the results (page 06, lines 155):

“We observed that in naïve animals, all of these parameters were similar in TNFR^-/- and C57BL/6 mice (Figures 2A-D, top panels and Figures 2E-H), with a slightly higher respiratory exchange rate in uninfected TNFR^-/- mice. In contrast, all the evaluated parameters were decreased in infected C57BL/6 mice compared to their naïve counterparts during the light and dark cycles. When we analyzed only infected mice, the alterations in all parameters were milder in TNFR^-/- compared to C57BL/6 mice (Figures 2A-D bottom panels and 2E-H).”

Figure 3. To give an idea of the main population of non-parenchymal cells, it will be helpful to clarify briefly how non-parenchymal cells from the liver of infected or uninfected mice were isolated.

We described in detail at Material and Methods (Page 19, Lines 566.)

Figure 3, B, C, D, G and Figure 4K and Figure 5 A and B - Semi-quantitative data through the densitometric analysis of western blots should be included in all figures.

Thank you for the suggestion. We now included the densitometric analysis for all Western blot results in Supplementary figure.

Figure 4. The author describes, "We observed that except for Hexokinase-3, the expression of mRNAs of glycolytic enzymes (Hexokinase-1, PFKP, and PKM) was increased in C57BL/6 but not TNFR-/- 8dpi." Sometimes, it is hard to understand which groups have been compared to some data. Be precise in describing the statistical analysis between the groups. It seems that those genes were increased in "infected C57BL/6 in comparison to uninfected mice, but not TNFR-/- 8-dpi. Moreover, even though the authors include statistic symbols "ι, ιι, ιιι" in other legends, there is no explanation about statistic symbols in the legend of Figure 4.

As mentioned above, we improved the descriptions of all figures in the legend, and when necessary in the main text describing the results.

Figure 5. The authors describe, "We found that GLUT1 protein and glycolysis (ECAR) was impaired, respectively, in monocytic cells and splenic CD11b+ cells from infected, as compared to uninfected HIF-1aΔLyz2 mice (Figures 5C-5E)." The GLUT-1 expression was inhibited in both cells compared to HIF-1afl/fl mice but not even close to impaired GLUT-1 expression. There is still a robust amount of GLUT-1 expression, and significantly higher when compared to cells from uninfected mice.

We tuned our statement to partially impaired, indicating that other host or parasite components maybe be also influencing GLUT-1 expression. In fact, we have recently published that IFNγ has also an important role in regulating GLUT1 expression in MO-DCs and this reference is mentioned in the text (page 10, line 291):

“We found that glycolysis (ECAR) and GLUT1 expression were impaired, though partially, in monocytic and splenic CD11b+ cells from infected HIF-1aΔLyz2 mice (Figures 5C-5E) compared to infected WT mice. The level of GLUT1 expression that is still maintained is likely due to other host or parasite factors, such as IFN-γ (Ramalho 2024).”

Figure 6. It is essential to have more information about the number of replicates in Figure 6A. However, there are just two dots replicates in the condition CD11b+ splenic cells from C57BL/6 stimulated with or without LPS (purple bars). It is essential to be precise regarding the number of experimental and biological replicates in each experiment and the statistical analysis that has been applied, including this group. Furthermore, the author concludes, "...these data demonstrated that RNI induces HIF-1α expression...." This conclusion needs a more careful description since no data supports that monocytic cells or splenic CD11b+ cells from iNOS-/- infected mice decrease stabilization of HIF-1αm using blotting, as shown in Figure 5 A.

As mentioned above the number of replicates for each experiment was included in the figure legends.

Minor Points.

Figure 3. "Hepatocytes have an important role in glucose uptake from the circulation, and they do this primarily through GLUT2 (38), whose mRNA expression was downregulated (Figure 3A) and protein expression unchanged in response to Pc infection (Figure 4K)." I suggest moving the Figure 4K to Figure 3 to make it easy to follow the data description.

We thank the reviewer for the suggestion. However, we chose to keep Figure 4K in Figure 4, as this panel includes data from TNF receptor deficient mice, and the analysis of TNF knockout models is first introduced and discussed in Figure 4. For clarity and consistency, we therefore maintained this panel within Figure 4.

Line 433. Replace iNOS for iNOS-/- mice.

iNOS is now replaced for iNOS-/- mice.

Reviewer #2 (Recommendations For The Authors):

The premise of the manuscript by Matteucci et al. is interesting and elaborates on a mechanism via which TNFa regulates monocyte activation and metabolism to promote murine survival during Plasmodium infection. The authors show that TNF signaling (via an unknown mechanism) induces nitrite synthesis, which (via yet an unknown mechanism), and stabilizes the transcription factor HIF1a. Furthermore, HIF1a (via an unknown mechanism) increases GLUT1 expression and increases glycolysis in monocytes. The authors demonstrate that this metabolic rewiring towards increased glycolysis in a subset of monocytes is necessary for monocyte activation including cytokine secretion, and parasite control.

The main goal of this work is to study the interplay of TNF/HIF1a/iNOs in the pathogenesis in an experimental model of malaria. To dissect the molecular mechanism by which TNF induces reactive nitrogen species and regulates HIFa expression is beyond the scope of our research. Nevertheless, there is a vast literature addressing these issues. We now include in the discussion a paragraph describing the main conclusion of these studies published previously (page 12, line 363):

"Previous studies have shown that TNF induces the production of RNI through the upregulation of iNOS via the NF-κB pathway (63, 64). TNF-mediated iNOS expression is critical for NO production, which in turn stabilizes HIF-1α by inhibiting prolyl hydroxylases (PHDs) even under normoxic conditions (58, 59). HIF-1α then upregulates the expression of glycolytic genes, including GLUT1 (22, 62).”

Major comments

Issues concerning novelty

Some of the reported observations are not novel. TNFa and TNFa signaling has been demonstrated to contribute to the release of certain cytokines, and to contribute to the control parasitemia (PMID: 10225939). TNFa has been shown to increase glucose uptake in tissues (PMID: 2589544). There is a textbook about the role of INOS during the pathogenesis of malaria, including its association with parasite control (https://link.springer.com/chapter/10.1007/0-306-46816-6_15). Furthermore, other mechanisms controlling glycemia during Plasmodium infection have been shown (PMID: 35841892). The authors should adequately discuss other papers which have reported some of their findings.

Thanks for the comments on previously existing literature. We are well aware of some of this earlier literature. Some of these earlier findings are mentioned in our manuscript. We emphasized these fundamental findings in the discussion, as requested (page 12, line 368):

“TNF has been described as a critical mediator in malaria, driving cytokine release and parasitemia control (PMID: 10225939). It also enhances glucose uptake in tissues, aligning with our findings of increased glycolysis in monocytes (PMID: 2589544). The role of iNOS in malaria is well documented. IFN-γ and TNF induced the production of NO, which inhibits parasite growth but can cause tissue damage and organ dysfunction, especially in severe malaria (Mordmüller et al., 2002). Recent studies also highlight the complexity of glycemia regulation during Plasmodium infection describing its role in modulating parasite virulence and transmission (PMID:35841892). These studies demonstrate the critical function of TNF and iNOS in immune responses against Plasmodium, aligning with our findings of this axis and metabolic rewiring that are essential for monocyte activation and outcome of Pc infection.”

The authors claim that "Reprogramming of host energy metabolism mediated by the TNF-iNOS-HIF1a axis plays a key role in host resistance to Plasmodium infection," and contributes significantly to their effector functions (particularly parasite clearing), and the systemic drop in glycemia observed during Pc infection. Although the authors show that TNFa does result in altered metabolism and increased GLUT1 levels in a subpopulation of monocytes, the evidence that TNFa-induced glylcolysis plays a key role in host resistance is correlative at best.

This is an important question. We did show that TNFR KO have higher parasitemia. But TNF is pleiotropic cytokine and has multiple roles on innate and acquired immunity. The experiment we have performed and helps to address this issue is the in vivo treatment with 2DG. We found that treatment with this inhibitor of glycolysis results in a increase of parasitemia. These results are now included in Figure 6.

When considering that the majority of monocytic populations are reduced in frequency and only a small subset (i.e., Monocyte-derived DCs) increase in frequency (Fig 3K) during Pc infection, this makes it very difficult to demonstrate that a cell population whose overall frequency reduces contributes significantly to the drop in glycemia during Pc infection. The authors should therefore include experiments that demonstrate that the inhibition of glycolysis induced by TNFa in monocytes is protective and/or contributes to a decrease in extracellular glucose. The authors could assess the impact of the loss of function of GLUT1 on activated monocytes and monocyte-derived DCs on glycemia upon TNFa stimulation.

We agree. We focused on monocytes and the derived inflammatory monocytes and MO-DCs. In fact, the frequency of monocytes, considering the inflammatory monocytes and MO-DCs, is increased both in spleen and liver. One interesting result is that the HIF1a Lysm KO mice has impaired metabolism, attenuated hypoglycemia and increased parasitemia (Figure 5). Nevertheless, we agree that our current data thus not proof that the glycemia is due to the consumption of glucose by the activated monocytes, and that these are the only cells with increased glucose consumption. This is now added to the discussion (page 13, line 395):

"Although the frequency of MO-DCs increases during infection, other cell populations may also contribute to glucose consumption. Further experiments, including the assessment of GLUT1 function in these populations, are needed to clarify their contribution to glucose consumption during infection."

Furthermore, in the current state of the manuscript, it is unclear how activated monocyte populations uptake glucose. The authors claim that glucose uptake by activated monocytes is GLUT1-dependent, however, glucose transport via GLUT1 is insulin-dependent. Since Plasmodium infection is associated with insulin resistance, and almost unquantifiable levels of insulin (PMID: 35841892), and TNFa itself induces insulin resistance (PMCID: PMC43887), it is unclear how the activated monocyte population uptakes glucose. If the authors consider TNFa to be sufficient for GLUT1 induction, in vitro experiments (TNFa+monocytes) could bolster this claim (and support that GLUT1 is induced in an insulin-independent mechanism.

There is significant evidences indicating that in contrast to GLUT4, induction of GLUT1 in mice is independent of insulin (PMID: 9801136). In our case, seems to be induced by the cytokines TNF and IFN𝛾(this study and Ramalho et al., 2024). We now performed experiments exposing monocytes to TNF and evaluating GLUT1 expression. The results indicate that monocytes exposed to TNF (100 ng/mL) for 18 hours from WT mice exhibited a significant increase in GLUT1 expression. This increase was comparable to the increased-GLUT1 phenotype observed in infected animals. The results of this experiment were included in the manuscript.

A text was included to the discussion to clarify the issue of insulin dependence of GLUT1 expression (page 13, line 388):

“GLUT1 expression is recognized as independent of insulin, in contrast to GLUT4 (PMID: 9801136). In our model, this regulation appears to be driven by pro-inflammatory cytokines, particularly TNF. Supporting this, our results show that in vitro stimulation with TNF, significantly increases GLUT1 expression in monocytes, accordingly to the ex vivo phenotype observed in infected animals.”

Alternative hypothesis which might explain their phenotypes

Figure 2 A-H: The metabolic effects of the genetic manipulations including INOS KO, TNFR KO, and HIF-1α∆Lyz2 could be explained by lesser disease morbidity owed to a reduction of inflammatory response during infection. Under this condition, the development of anorexia will not be as profound in the knock-outs compared with wild-type littermate controls, since anorexia of infection is tightly linked to the magnitude of inflammatory response. Accordingly, infected knock-out animals can keep eating, which presumably impacts glycemia, maintenance of core body temperature, and overall energetics of infected mice. The authors should exclude this possibility.

We consider this possibility and the discussion now elaborates about this alternative hypothesis. We believe, that these two mechanisms are not mutually exclusive (page 16, line 474):

“Although restored physical activity, food consumption and energy expenditure in knockout mice may contribute to the observed systemic metabolic parameters by altering energy balance, these effects are not mutually exclusive with the TNF-driven, cell-intrinsic metabolic mechanisms described here.”

Minor comments

The authors showed increased parasitemia upon TNFR and HIF1a depletion in the LyZ2 compartment. The same was observed upon organismal INOS depletion. This raises the question of whether the TNFHIF-INOS signaling axis is adaptive or maladaptive during Pcc infection. The authors should show host survival in mice lacking TNFR and HIF1a in the LyZ2 compartment, and in mice lacking INOS (presumably, they have these data).

Despite the fact the various knockout mice have increased parasitemia and signs of disease, they all survive the infection. This is now included in the Figure legends.

Are the higher tissue glucose levels specific to the liver and the spleen or this is a more general event? Have the authors looked at other organs?

We now added the results of glucose uptake in the muscle and adipose tissues in figure 2. The fact that the glucose uptake is not increased in muscle and adipose tissue, further suggest that the increased glucose uptake in this model is insulin independent.

Figure 1F: All core body temperatures are within the physiological range, i.e., >36 degrees C. This makes it unclear why the authors regarded this as hypothermia. The authors should present experiments demonstrating the development of hypothermia in Figure 1F, as they claim this.

Temperature changes in mouse kept in animal house have been an issue discussed in the field. It is clear, however, that early in the morning (end of active period) mice have torpor. Lower temperature and physical activity.

In Figure 4, since the authors already suggested that extra-hepatic cells, and not the liver parenchyma, contribute to glucose uptake, the authors should clarify why they analyzed the whole liver in Figure 4, and not extra-hepatic cells. Furthermore, the authors should quantify the hepatic monocytic population in non-infected versus infected wild-type animals.

The reason we used whole liver, is that the number of non-parenchymal cells obtained from liver is limited for Western blot analysis. We thought that was important to show that expression of GLUT1 was decreased in the liver of TNFR KO mice. Nevertheless, the level of TNFR expression in different cell types in the liver was shown by flow cytometry. In addition, we performed the WB with cells extracted from the spleen, where lymphoid and myeloid cells are more abundant.

Line 87: Phagocytizing parasitized what?

This has been corrected in the manuscript.

Line 111 Define RNI before being used.

Is there a gender disparity in the TNFR KO phenotype? If yes, the authors should comment about this in their discussion.

This has been defined and addressed in the manuscript

Line 192: Did the authors mean 3B??

In 3M, please plot monocytes from uninfected animals.

The plot of uninfected animals are now included in Figure 3M

Line 390 Remove the extra dash in HIF1a.

Extra dash has been removed.

Line 397 Define RA

RA is now defined.

Author response:

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

We thank the reviewers for their careful reading of our manuscript and for the constructive and insightful feedback. In response, we performed several new experiments and analyses that significantly strengthen the study. First, we addressed the important question of optoLARG recruitment dynamics by generating a new cell line expressing optoLARG-mScarlet3 together with paxillin-miRFP, enabling us to directly quantify the dynamics of the optogenetic activator at focal adhesions and the plasma membrane. Second, we introduced a quantitative modeling framework to analyze RhoA activity dynamics during transient optogenetic stimulation. Using the measured optoLARG kinetics as input, we fitted activation and deactivation parameters for both WT and DLC1 KO cells, revealing a loss of negative feedback regulation in the KO condition. Together, these additions clarify the temporal relationships between optogenetic activation, RhoA signaling, and biosensor responses, and provide a more rigorous, mechanistic interpretation of our data. We rewrote large parts of the discussion section to reflect this new information.

Below, we provide detailed, point-by-point responses to all reviewer comments.

Recruitment dynamics optoLARG

Reviewer #1:

Public Review:

For the optogenetic experiments, it is not clear if we are looking at the actual RhoA dynamics of the activity or at the dynamics of the optogenetic tool itself.

Recommendations for the authors:

For the transient optogenetic activations at FA and PM, it would be great to have one data set where the optoLARG is fused to a fluorescent protein, for example, mCherry, while FAs would be marked with paxillin-miRFP (by transient transfection to avoid making a new stable cell line). The dynamics of the optogenetic activator should be the same (on and off rates), but it can be possible that the activator is retained at FA for example. Such an experiment would help the understanding of the differential observed dynamics, where several timescales are involved: the dynamics of the opto tool, the dynamics of RhoA itself, and the dynamics of the biosensor.

We agree with the reviewers, this is an essential control for this manuscript and the cell line will be useful in future studies. We developed a new construct containing with the recruitable SSpB domain tagged in red (optoLARG-mScarlet3) compatible with the iLid system, and paxilin-miRFP to locate the focal adhesions. From previous experiments we know that the anchor part of optoLARG system is distributed evenly across the cell membrane and is not affected by cytoskeletal structures like focal adhesions. As for the recruitable part of the optoLARG system, that translocates from the cytosol to the membrane upon blue light stimulation, we illuminated focal adhesion and non-focal adhesion regions, and quantified optoLARG dynamics. The same scripts were used for automated stimulation and analysis as were used for the rGBD recruitment experiments. We illustrate these results in the new Suppl. Fig S3. We found no significant difference in recruitment dynamics between focal adhesion/non-focal adhesion regions (Fig. S3B). We found the optoLARG dynamics fits well with inverse-exponential during recruitment under blue light stimulation, and exponential decay after blue light stimulation (disassociation phase), consistent with the expected iLID dynamics (Fig S3C). This experiment is described in detail at the end of the section "Optogenetic interrogation of the Rho GTPase flux in WT and DLC1 KO cells" (Lines 303-320). We then went on to use the optoLARG dynamics as input for the models describing RhoA activity dynamics (see next comment). This should help to untangle the measured RhoA dynamics from the dynamics of the optogenetic tool.

Quantitative analysis RhoA activity dynamics

Public Review:

There is no model to analyze transient RhoA responses, however, the quantitative nature of the data calls for it. Even a simple model with linear activation-deactivation kinetics fitted on the data would be of benefit for the conclusions on the observed rates and absolute amounts.

Recommendations for the authors:

[...] for the transient optogenetic experiments, it would be great to make a simple model, or at least to fit the curves with an on rate, an off rate, and a peak value. This will clarify the conclusions drawn for the experiments. For example, the authors claim that they observe an increased Rho activation rate in DLC1 KO cells (see sections "Optogenetic interrogation of the Rho GTPase flux in WT and DLC1 KO cells" and "Discussion") but the rate is not well-defined. One can have two curves with the same activation rate but one that peaks higher (larger multiplicative prefactor) and it would resemble the presented data. This being said, the higher deactivation rate in DLC1 KO cells is evident from the data.

We agree that a quantitative analysis and model would improve our understanding of the data. We fit the activation/deactivation kinetics and provide the values in the chapter "Optogenetic interrogation of the Rho GTPase flux in WT and DLC1 KO cells" (Lines 287-299). We then modeled the RhoA activity dynamics at focal adhesions and at the plasma membrane after transient optogenetic stimulation using a system of ODEs, using the new measurements of optoLARG kinetics as activation input. We find a close fit for the experimental data, with WT following classic Michaelis-Menten dynamics. Interestingly, when fitting the DLC1-KO data with the same model as for WT, the parameter modeling the negative feedback loop (active RhoA recruiting a GAP) is set to zero; in other words, the factor that deactivates RhoA is present at a constant concentration. We added an additional main Figure 5 describing the models and fits, and added a new Results section "Modeling indicates loss of negative RhoA autoregulation in DLC1-KO cells" (Lines 326-378), and also updated the Methods and Discussion section of the paper accordingly. We use the findings to more clearly ground the mathematical terms used to describe our results.

Error figure 6E

Recommendations for the authors:

The scheme presented in Figure 6E is not supported by the data and should be modified. In this scheme, the authors show a strongly delayed peak in control cells versus DCL1 KO cells, whereas in the data the peaks appear to be at similar time points. Similarly, the authors show a strongly decreased rate of activation, whereas the initial rates appear identical in the data.

The delayed peak we illustrated is an error, we thank the reviewers for catching it. The decreased rate of deactivation and activation, although exaggerated in the scheme, is however present in the data (and is now quantified, see answer above). We updated the figure accordingly (now Fig. 7E in the manuscript).

Clarification term "signaling flux"

Recommendations for the authors:

It would be nice to define more precisely several terms that are used throughout the manuscript. For example, could the authors define what they mean by "signaling flux"? Is it the temporal derivative of the Rho levels? Or the spatial derivative?

We agree that this was not clear in the previous version of the manuscript. We refer to "signaling flux" as the continuous cycle of RhoA activation by GEFs and inactivation by GAPs, processes that persist even when bulk RhoA activity appears steady, as introduced by Miller & Bement (2009). We now explicitly define "signaling flux" in the abstract (Lines 20-24).

See: Miller, Ann L., and William M. Bement. "Regulation of cytokinesis by Rho GTPase flux." Nature cell biology 11.1 (2009): 71-77. https://doi.org/10.1038/ncb1814

Recommendations for the authors:

Also (see above) it would be nice to define precisely what are the rates: the activation rate is in general the k_on of a reaction scheme, but it will differ from the observed rate given by a biosensor. For example, with a k_on and a k_off the observed rate toward the steady-state will be given by the sum of the activation and deactivation rates. In the manuscript, the authors do not make the distinction between the activation rate with the rate of increase of the biosensor which is confounding for the reader and for the interpretation of the data.

We update the results section to make this distinction more clear (Lines 288-300), and add a note explicitly highlighting the difference between biosensor signal dynamics and the underlying RhoA activation/deactivation rates (Lines 298-300). In addition, our newly introduced model helps disentangle the combined activation/deactivation rates into distinct GEF and GAP activity parameters.

Improvements to figure 3

Minor recommendation:

In Figures 3 B and D, the stars (statistical differences) are not visible. It would be good to make them bigger or move them above the graphs.

Thank you! We updated the graphics.

Other changes

Additional panel (Figure 5D) showing paxillin intensity does not change after weak optogenetic stimulation, to better illustrate the weak stimulation regime that does not trigger FA reinforcement (contrasting Figure 7). Additional small layout changes to Figure 5.

Addition of authors that contributed to the revisions

Author response:

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

eLife Assessment

This study represents an important advance in our understanding of how certain inhibitors affect the behavior of voltage gated potassium channels. Robust molecular dynamics simulation and analysis methods lead to a new proposed inhibition mechanism with strength of support being mostly convincing, and incomplete in some aspects. This study has considerable significance for the fields of ion channel physiology and pharmacology and could aid in development of selective inhibitors for protein targets 

We are encouraged by this favorable assessment and thank editors and reviewers for their constructive feedback and recommendations. We trust that the revisions made to the manuscript will clarify the aspects that had been perceived to be incomplete.

Reviewer #1 (Public review):

Summary: 

This study seeks to identify a molecular mechanism whereby the small molecule RY785 selectively inhibits Kv2.1 channels. Specifically, it sought to explain some of the functional differences that RY785 exhibits in experimental electrophysiology experiments as compared to other Kv inhibitors, namely the charged and non-specific inhibitor tetraethylammonium (TEA). This study used a recently published cryo-EM Kv2.1 channel structure in the open activated state and performed a series of multi-microsecond-long all-atom molecular dynamics simulations to study Kv2.1 channel conduction under the applied membrane voltage with and without RY785 or TEA present. While TEA directly blocks K+ permeation by occluding ion permeation pathway, RY785 binds to multiple nonpolar residues near the hydrophobic gate of the channel driving it to a semi-closed non-conductive state. This mechanism was confirmed using an additional set of simulations and used to explain experimental electrophysiology data.

Strengths:

The total length of simulation time is impressive, totaling many tens of microseconds. The study develops forcefield parameters for the RY785 molecule based on extensive QM-based parameterization. The computed permeation rate of K+ ions through the channel observed under applied voltage conditions is in reasonable agreement with experimental estimates of the singlechannel conductance. The study performed extensive simulations with the apo channel as well as both TEA and RY785. The simulations with TEA reasonably demonstrate that TEA directly blocks K+ permeation by binding in the center of the Kv2.1 channel cavity, preventing K+ ions from reaching the SCav site. The conclusion is that RY785 likely stabilizes a partially closed conformation of the Kv2.1 channel and thereby inhibits the K+ current. This conclusion is plausible given that RY785 makes stable contact with multiple hydrophobic residues in the S6 helix. This further provides a possible mechanism for the experimental observations that RY785 speeds up the deactivation kinetics of Kv2 channels from a previous experimental electrophysiology study.

Weaknesses:

The study, however, did not produce this semi-closed channel conformation and acknowledges that more direct simulation evidence would require extensive enhanced-sampling simulations. The study has not estimated the effect of RY785 binding on the protein-based hydrophobic pore constriction, which may further substantiate their proposed mechanism. And while the study quantified K+ permeation, it does not make any estimates of the ligand binding affinities or rates, which could have been potentially compared to the experiment and used to validate the models. 

As stated in the original manuscript, we concur that the mechanism we propose remains hypothetical until further studies of the complete conformational cycle of the channel are conducted. The recently determined structure of a Kv2.1 channel in the closed state (Mandala and MacKinnon, PNAS 2025) presents an excellent opportunity to do so. Indeed, a cursory analysis of that structure shows that a Pro-Ile-Pro motif in helix S6 marks the position of the intracellular gate, where the pore domain constricts maximally (aside from the selectivity filter). As illustrated in Fig. 5, this motif is precisely where the benzimidazole and thiazole moieties of RY785 bind in our simulations. The mechanism we outline in Fig. 7 thus seems very plausible, in our view; that is RY785 occludes the K⁺ permeation pathway before the pore domain reaches the closed conformation, explaining the observed electrophysiological effects (see Discussion). The Discussion has been revised to note the recent discovery of the aforementioned structure, its implications for the mechanism we propose, and the opportunities for further research that are now open.

Reviewer #3 (Public review):

Summary:

In this manuscript, Zhang et al. investigate the conductivity and inhibition mechanisms of the Kv2.1 channel, focusing on the distinct effects of TEA and RY785 on Kv2 potassium channels. The study employs microsecond-scale molecular dynamics simulations to characterize K+ ion permeation and compound binding inhibition in the central pore. 

Strengths:

The findings reveal a unique inhibition mechanism for RY785, which binds to the channel walls in the open structure while allowing reduced K+ flow. The study also proposes a long-range allosteric coupling between RY785 binding in the central pore and its effects on voltage-sensing domain dynamics. Overall, this well-organized paper presents a high-quality study with robust simulation and analysis methods, offering novel insights into voltage-gated ion channel inhibition that could prove valuable for future drug design efforts.

Weaknesses:

(1) The study neglects to consider the possibility of multiple binding sites for RY785, particularly given its impact on voltage sensors and gating currents. Specifically, there is potential for allosteric binding sites in the voltage-sensing domain (VSD), as some allosteric modulators with thiazole moieties are known to bind VSD domains in multiple voltage-gated sodium channels (Ahuja et al., 2015; Li et al., 2022; McCormack et al., 2013; Mulcahy et al., 2019).

As noted in the manuscript, we designed our simulations to explore the possibility that RY785 binds within the pore domain, because TEA and RY785 are competitive and TEA is known to bind within the pore. That RY785 did in fact spontaneously and reproducibly bind within the pore was however not a predetermined outcome; if the site of interaction for the inhibitor was elsewhere in the channel, the simulation would not have shown a stable associated state, which would have prompted us to examine other possible sites, including the voltage sensors. It was also not predetermined or foreseeable a priori that the mode of interaction we observed in simulation provides a straightforward rationale for the electrophysiological effects of RY785. Based on our results, therefore, we believe that RY785 binds within the pore of Kv2. As stated by the reviewer, other allosteric modulators are known to bind instead to the sensors; to our knowledge, however, there is no precedent of a small-molecule inhibitor that simultaneously acts on the sensors and the pore domain. We therefore believe that future studies should focus on corroborating or refuting the mechanism we propose, through additional experimental and computational work; if, contrary to our claim, RY785 is found not to bind to the pore domain, it would be logical to explore other possible sites of interaction, as the reviewer suggests. The Discussion has been modified to address this point.

(2) The study describes RY785 as a selective inhibitor of Kv2 channels and characterizes its binding residues through MD simulations. However, it is not clear whether the identified RY785-binding residues are indeed unique to Kv2 channels.

To clarify this question, we have included a multiple sequence alignment as Supplementary Figure 1; the revised manuscript refers to this figure in the Discussion section. The alignment reveals that the cluster of residues forming contacts with RY785 (Val409, Pro406, Ile405, Ile401, and Val398) is indeed specific to Kv2.1. Among Kv channels, Kv3.1 and Kv4.1 exhibit the greatest similarity to Kv2.1 at these positions, but they differ in a crucial substitution: Ile405 in Kv2.1 is replaced by Val. This replacement shortens the sidechain, undoubtedly reducing the magnitude of the hydrophobic interaction between inhibitor and channel (Val is approximately 6 kcal/mol, i.e. 1,000 times, more hydrophilic than Ile). Kv5.1 differs from Kv2.1 at two positions: Pro406 is replaced by His, and Val409 by Ile. The introduction of His abolishes the hydrophobic interaction at that position, and the need for hydration likely perturbs all adjacent contacts with RY785. Lastly, Kv6-Kv10 and Cav channels feature entirely different residues at these positions. Consistent with these findings, a recent study by the Sack lab (https://elifesciences.org/articles/99410) has demonstrated that Kv5, Kv6, Kv8, and Kv9 pore subunits confer resistance to RY785, while a high-throughput electrophysiological study carried out by Merck (Herrington et al., 2011) reported that RY785 shows no significant activity against Cav channels. The sequence alignment offers a simple interpretation for these experimental observations, namely that RY785 is recognized by Kv2 channels through the abovementioned hydrophobic cluster within the pore domain.

(3) The study does not clarify the details, rationale, and ramifications of a biasing potential to dihedral angles.

We refer the reviewer to published work, for example Stix et al, 2023 and Tan et al, 2022. We provide additional comments below.

(4) The observation that the Kv2.1 central pore remains partially permeable to K+ ions when RY785 is bound is intriguing, yet it was not revealed whether polar groups of RY785 always interact with K+ ions.

We detected no persistent specific interactions between RY785 and the permeant K+ ions.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

The manuscript describes atomistic molecular dynamics (MD) simulations of a voltage-gated potassium channel Kv2.1 using its cryo-EM structure in the open activated state and its inhibition by a classical non-specific cationic blocker tetraethylammonium (TEA) as well as a novel selective inhibitor RY785. Using multi-microsecond-long all-atom MD runs under the applied membrane voltage of 100 mV the authors were able to confirm that the channel structure represents an open conducting state with the computed single-channel conductance lower than experimental values, but still in the same order of magnitude range. They also determined that both TEA and RY785 bind in the channel pore between the cytoplasmic hydrophobic gate and narrow selectivity filter (SF) region near the extracellular side. However, while TEA directly blocks a knock-on K+ conduction by physically obstructing ion access to the SF, the mechanism of action of RY785 is different. It does not directly prevent K+ access to the SF but rather binds to multiple residues in the hydrophobic gate region, which effectively narrows a pore and drives the channel toward a semi-closed nonconductive conformation, which might be distinct from one with the deactivated voltage sensors and closed pore observed at hyperpolarized membrane potentials. However, additional studies beyond the scope of this work might be needed to fully establish this mechanism as suggested by the authors.

The manuscript is written very well and represents a significant advance in the field of ion channel research. I do not have any major issues, which need to be addressed. However, I have several suggestions.

For the apo-channel K+ conduction MD simulation under the applied voltage, the authors seem to observe mostly a direct or Coulomb knock-on mechanism across the SF with almost no water copermeation. This is in line with computational electrophysiology studies with dual membrane setup by B. de Groot and others but in disagreement with multiple previous studies by B. Roux and others also using applied electric field and CHARMM force fields as in the present study. I wonder why the outcomes are so different. Is it related to the Kv2.1 channel itself, a relatively small applied electric field used (corresponding to a membrane potential of 100 mV vs. 500-750 mV used in many previous simulations), ion force field (e.g., LJ parameters), or some other factors? Could weak dihedral restraints on the protein backbone and side chains contribute to this mechanism? I also wonder if the authors might have considered different initial SF ion configurations. Related to that, I wonder if the authors observed any SF distortions in their simulations including frequently observed backbone carbonyl flipping and/or dilation/contraction.

We are aware of these discrepancies between published simulation studies, but cannot offer a satisfactory explanation, beyond speculation. The reviewer is correct that the mechanism of ion permeation we observe is comparable to that reported by de Groot, as we noted in Tan et al, 2022 and Stix et al, 2023. Neither in this nor in those previous studies did we observe any persistent distortions of the selectivity filter – but that outcome was expected by construction. The weak biasing potentials acting on the mainchain dihedral angles allow for local fluctuations but not a persistent deformation, relative to the conductive form determined experimentally.

For MD simulations with the ligand present, I wonder if the authors can comment on the effect of the ligand especially RY785 on the pore size or more importantly size of the hydrophobic gate. The presence of the ligand itself would definitely result in a narrower pore, but I also wonder if this would also lead to a rearrangement of pore sidechain and/or backbone residues, which would lead to a narrower pore from a protein itself thus confirming the proposed mechanism of driving the channel towards a semi-closed state. It is easy to compute but I wonder if the presence of weak dihedral restraints may preclude this analysis.

Yes, while the simulation design used in this study allows for local fluctuations in the mainchain structure and nearly unrestricted sidechain dynamics, changes in either the secondary or tertiary structure of the channel are strongly disfavored. This approach is thus sufficient to examine ligand binding or ion flow in the microsecond timescale but not channel gating. In the revised version of the Discussion, we outline a roadmap for future computational studies of that gating process, on the basis of the open-channel structure we used and the recently determined structure of the closed state.

The authors state that RY785 does not block K+ ion, but it does significantly slow the rate of K+ ion access to the pore Scav site. Is this not a part of the mechanism for inhibition of the channel? The authors seem to focus on the primary mechanism of inhibition as the RY785 promoting channel closing, but would it not also reduce K+ current in the open state by slowing the rate of K+ entry into the cavity and selectivity filter? The authors should address this point in the text. I am also somewhat confused that in the MD simulations performed by the authors, there is still some K+ conduction with RY785 in the pore, which is not in 100% agreement with electrophysiology experiments. Does it mean that the channel in the simulations has not yet reached that semiclosed state or a reduced K+ conduction is not observed experimentally?

The salient experimental observation is RY785 abrogates K+ currents through Kv2 channels (Herrington et al, 2011; Marquis et al, 2022). In our view, that observation can be explained in one of two ways: either RY785 completely blocks the flow of K+ ions across the channel while the pore domain remains in the conductive, open state – like TEA does – or RY785 induces or facilitates the closing of the channel, thereby abrogating K+ flow. The fact that we observe K+ flow while RY785 is bound to the channel is therefore not in disagreement with the electrophysiological measurements, but it does rule out the first of those two possible interpretations of the existing experiments. As it happens, the second possible explanation, i.e. that RY785 facilitates the closing of the pore domain, also provides a rationale for another puzzling experimental observation, namely that RY785 shifts the voltage dependence of the currents produced by the voltage sensors as they reconfigure to open or close the intracellular gate.

Also, I wonder if the authors considered that since there are 4 potential equivalent sites in the pore (although, overlapping) more than one RY785 might be needed to prevent K+ conduction, even though the experimental Hill coefficient of ~1 does not indicate cooperativity.

Admittedly, our simulation design was based on the premise that only one RY785 molecule might be recognized within the pore. Based on the outcome of the simulations, we are confident that this assumption was valid, as the binding pose that we identified rules out multiple occupancy – which would be indeed consistent with a Hill coefficient of ~1.

I also wonder if the authors considered estimating ligand binding affinities and/or "on" rates from their simulations to have a more direct comparison with experiments and test the accuracy of their models. There are multiple enhanced sampling techniques allowing to do that, although it can be a study on its own.

We thank the reviewer for this suggestion, which we will consider for future studies.

The authors also discussed that they could not study Kv2.1 deactivation in a reasonable simulation time. Indeed it is very challenging but they should cite previous studies e.g. 2012 Jensen et al paper (PMID: 22499946) on this subject. There are structures of Kv channels with the deactivated voltagesensing domains (VSDs) available, e..g of EAG1 channel (PDB 8EP1), although they do not have a domain-swapped architecture. There are structural modeling approaches including AlphaFold, which can be potentially used to get a Kv2.1 structure with deactivated VSDs, and targeted MD, string method etc. can be used to study transition between different states with and without bound ligands.

As noted, a structure of a Kv2 channel with a closed pore has now been determined experimentally. In the revised Discussion, we comment on what this structure tells us about the mechanism of inhibition we propose, and how it could be leveraged in future studies.

The authors should be commended for doing a thorough QM-based force field parameterization of RY785. However, a validation of the developed force field parameters is lacking. In terms of QM validation, a gas-phase dipole moment can be compared in terms of direction and magnitude (it's normal to be overestimated to implicitly reflect solvent-induced polarization). If there are any experimental data available for this compound, they can be tested as well.

We agree with the reviewer that forcefield validation is important, but to our knowledge no experimental data exists for RY785 to compare with, such as hydration free energies. We did however compare the gas-phase dipole moment computed with QM and with the MM forcefield we developed based on atomic charges optimized to reproduce QM interactions with water. The MM model yields a gas-phase dipole moment of 3.94 D, which is 20% greater than the QM dipole moment, or 3.23 D. That deviation is within the typical range for electroneutral molecules (Vanommeslaeghe et al, 2010), and as the reviewer notes, reflects the solvent-induced polarization implicit in the derivation of atomic charges. As shown in Author response image 1, the orientation of the dipole moment calculated with MM (right, blue arrow) is also in good agreement with that predicted with QM (left)

Author response image 1.

(1) p. 3 "the last two helices in each subunit" -> "the last two transmembrane helices in each subunit".

Thanks. Corrected.

(2) p. 5 "and therefore do not cause large density variations e.g. 100-fold or greater.". I would be more specific here and indicate what are the actual variations in density or free energy encountered and how they are compared e.g. with thermal fluctuations (~kT).

Thanks. The exact variations in K+ density had been included in the original manuscript, in Fig. 2C, but we failed to refer to this figure at this point in the description of the results. The ion density is plotted in a log scale to facilitate conversion to free-energy units. Corrected.

(3) p. 6 Figure 1 caption "and along the perpendicular to the membrane" -> "perpendicular to the membrane normal"?. "The channel is an assembly of four distinct subunits (in colors);" -> "The channel is an assembly of four identical subunits (distinct by colors);". I would use the same protein coloring method in panels B and C as was used in panel A.

Thanks. Corrected as needed.

(4) p. 6 Figure 2 In panel B I would appreciate a representative complete ion permeation event trace. In panel C caption I would indicate corresponding sites "S0-S4, Scav" for each residue mentioned. I also would not use gray color for site names in the figure.

We appreciate the suggestion, but believe the figure is clear as is. Panel B is meant to focused on the mechanism of knock-on. Panel A includes numerous complete permeation events. 

(5) p. 7 Figure 3 caption. Please indicate which atoms of residues T373 and P406 were used to define SF and gate positions. Chemical structures of both TEA and RY785 would be useful. In panels C and F channel interacting residues (if any) would be helpful to show.

The revised caption clarifies that the positions of T373 and P406 are represented by their carbonalpha atoms. A close-up view of the structures of TEA and RY785 is included in the Supplementary Information section.

(6) p. 8. Figure 4 caption. Please indicate if N atoms ere used for density maps in panels B and C, and which value of the density was used to show meshes. In panel A please indicate what are the units of the density shown by color maps. 

The caption has been revised to clarify these questions.

(7) p. 9 "inside the protein" -> "inside the channel pore".

Thanks. Corrected.

(8) p. 10 "which lines the cavity" -> "which lines the water-filled cavity"

We appreciate the suggestion but believe the wording is clear as is.

(9) p.10 Fig. 5. It would be helpful to distinguish residues from different chains e.g. by different colors rather than using different colors for different residues. The S atom in RY785 is hard to recognize due to the yellow color used for C atoms. Figure 5B is very confusing. It is not clear what this plot represents. For instance, what does it mean that Pro405 has ~10 contacts in 20% of simulation snapshots? Does it mean 10 C..C/S interactions within 4.5 A? I am not sure what the value of this is. I think a bar or radar chart plot showing % of contacts with one, two, or more residues of each type would be more helpful. 

Thanks. The revised caption ought to clarify how to interpret the plot.

(10) p. 12 "Due to its 2-fold molecular symmetry". TEA has a tetrahedral point group or Td symmetry. It has several two-fold rotational axes though. 

Thanks. Corrected.

(11) p. 12 "it prevents K+ ions in the cytoplasmic space from destabilizing the K+ ions that reside in the selectivity filter" I am not sure if this statement is entirely accurate as there might be destabilization of a multi-ion SF configuration not ions per see.

We believe this statement is clear as is.

(12) p. 13 Fig. 7 caption "includes non-conductive or transiently inactivated states" - I am not sure what "transiently inactivated state" is as inactivation is a specific term used in ion channel research and it does not seem to be explicitly considered in this study.

A reference has been included in the caption for readers interested in the process of inactivation.

(13) p. 14 "the net charge of these constructs is thus zero". This would depend on the number of basic and acidic residues in the protein. 

Yes, it does – and as a result the construct we model has a net zero charge.

(14) p. 14 I wonder if the protein was constrained or heavily restrained during MARTINI membrane building and equilibration procedure. Otherwise, C-alpha mapping would be problematic and clashes with lipid membrane atoms might take place as well.

It was indeed. When a protein is simulated using the MARTINI coarse-grained forcefield, its fold must be preserved through a network of strong ‘virtual’ bonds between adjacent carbon-alpha atoms. This is standard practice so we do not believe it requires further explanation.

(15) p. 15 PME - please spell out and provide reference.

Corrected.

(16) p. 15 "with a smooth switching function" - is it a special or standard switching function? Also, was it used for energy or forces? 

The switching function brings both forces and energies to a value of zero at the cut-off value, smoothly. We refer the reviewer to the NAMD manual for further details.

(17) p. 15 '𝑘 = 1 𝑘B𝑇.' Please confirm that there is a factor of "1" there, which can be actually skipped if this is the case. 

The value of k = 1 KBT is correct.

(18) p. 15. Please cite PMID: 22001851 for the transmembrane electric field application technique.

Corrected.

(19) p. 15 "and CHARMM36m" -> "and CHARMM36m force field". 

Corrected.

(20) p. 16 "the four proteins subunits" -> "the four protein subunits". 

Corrected.

(21) p. 16. Please provide the reference for CGenFF. It's reference 49. 

Corrected.

Supporting Information (SI): CGenFF is misspelled in multiple figure captions in the SI. All potential energy scans indicate "angle", but some are bond angles while others are dihedral angles. Using subscripts for atom numbers is confusing and does not match the numbering scheme used in Fig. S1. So, please use the same style of numbering throughout, e.g. C46-C42-N43 (without subscripts). Please label the X and Y axes in Figsures S2-S19 and S21. In Figure S22 please perform a linear regression analysis and/or compute Pearson correlation coefficients and indicate trend lines. Table S1. It would be good to compute RMS or mean unsigned errors to get an idea about accuracy. Also, please indicate if reference QM values were scaled by 1.16 for energies or offset for distances. 

The Supplementary Information has been corrected. We thank the reviewer for their detailed feedback. 

Reviewer #3 (Recommendations for the authors):

(1) The study needs to consider the possibility of multiple binding sites for RY785, particularly given its impact on voltage sensors and gating currents. Specifically, the potential for allosteric binding sites in the voltage-sensing domain (VSD) should be assessed, as some allosteric modulators with thiazole moieties are known to bind VSD domains in multiple voltage-gated sodium channels (Ahuja et al., 2015; Li et al., 2022; McCormack et al., 2013; Mulcahy et al., 2019). Molecular docking and/or MD simulations could quickly test this hypothesis. If this hypothesis is not true, a comprehensive search can exclude such a possibility, which can also confirm the long-range allosteric coupling between RY785 binding in the central pore and voltage-sensing domain dynamics. 

Please see our response above.

(2) The authors describe RY785 as a selective inhibitor of Kv2 channels and characterize its binding residues through MD simulations. To support this claim, Figure 5 needs to include a multiple sequence alignment with other Kv channels. This would help demonstrate whether the identified RY785-binding residues are indeed unique to Kv2 channels.

Please see our response above.

(3) The study applies a biasing potential to 𝜙, 𝜓, and 𝜒1 dihedral angles. Please clarify:

(a) Is this potential solely to prevent selectivity filter collapse/degradation, as mentioned in a previous D. E. Shaw Research publication (Jensen et al., 2012)?

Yes, that is correct.

(b) If it applies to all amino acids, can this potential prevent other changes, such as in the voltagesensing domain?

Yes, that is correct.

(c) What specific "large-scale structural changes" does this potential preclude? 

For example, it would preclude the spontaneous degradation of the secondary or tertiary structure of the protein. We have revised the Methods section to make these points clearer. 

(d) Given that such biasing potentials on backbone dihedral angles can decrease conformational flexibility, and considering that Kv channel permeability/conductivity could be highly sensitive to filter flexibility, what insights can you provide about the impact of the force constant k on channel conductivity?

In previous studies based on an identical methodology (Stix et al, 2023; Tan et al, 2022), we have observed good agreement between calculated and experimental conductance values – at least as good as can be hoped for, when all approximations are considered. Based on the data presented in those studies, we have no reason to believe our methodology inhibits the permeability of the channel, which is logical as the local structural fluctuations required for K+ flow across the selectivity filter are not impaired, by definition. To the contrary, the fact that these weak biasing potentials make the conductive form of the filter the most favorable state in simulation enable a clear-cut analysis of conductance under plausible simulation conditions, both in terms applied voltage and K+ concentration. We refer the reviewer to the abovementioned studies for further details and a discussion of this subject.

(4) The observation that the Kv2.1 central pore remains partially permeable to K+ ions when RY785 is bound is intriguing. Given the compact nature of the central cavity when RY785 is bound, it would be valuable to investigate whether polar groups of RY785 (e.g., nitrogens from the amide, benzimidazole, and thiazole moieties) always interact with K+ ions. Characterizing these interactions could inform the design of similar compounds with differential modulation effects.

We examined this possibility and detected no convincing interaction patterns between RY785 and K+ ions – logically, inhibitor and ions are in close proximity while residing concurrently within the pore, but we detected no evidence of specific interactions.

Minor points:

It is strongly recommended that the refined force field parameters for RY785 be shared as a separate supplementary file in CHARMM force field format. This addition would be valuable for the scientific community, allowing other researchers to use or compare these parameters in future studies.

We agree entirely. Upon publication of the VOR for this article the forcefield parameters for RY785 will be made freely available for download at https://github.com/Faraldo-Gomez-Lab-atNIH/Download.

The study uses a KCl concentration of 300 mM, which exceeds typical intracellular K+ levels. While this may be intentional to enhance K+ permeation probability, a brief justification for this choice should be included in the Methods section.

Yes, what motivated this choice in this and in our previous studies of K+ channels was the expectation of a greater number of permeation events, for a given simulation length, and therefore greater confidence (i.e. statistical significance) in the observed ion conductance, or in the degree to which it might be inhibited by a blocker. It worth noting that 300 mM KCl, while atypical in the intracellular environment, is often used in electrophysiological studies. The Methods section has been amended to clarify this point.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

Persistence is a phenomenon by which genetically susceptible cells are able to survive exposure to high concentrations of antibiotics. This is especially a major problem when treating infections caused by slow growing mycobacteria such as M. tuberculosis and M. abscessus. Studies on the mechanisms adopted by the persisting bacteria to survive and evade antibiotic killing can potentially lead to faster and more effective treatment strategies.

To address this, in this study, the authors have used a transposon mutagenesis based sequencing approach to identify the genetic determinants of antibiotic persistence in M. abscessus. To enrich for persisters they employed conditions, that have been reported previously to increase persister frequency - nutrient starvation, to facilitate genetic screening for this phenotype. M.abs transposon library was grown in nutrient rich or nutrient depleted conditions and exposed to TIG/LZD for 6 days, following which Tnseq was carried out to identify genes involved in spontaneous (nutrient rich) or starvationinduced conditions. About 60% of the persistence hits were required in both the conditions. Pathway analysis revealed enrichment for genes involved in detoxification of nitrosative, oxidative, DNA damage and proteostasis stress. The authors then decided to validate the findings by constructing deletions of 5 different targets (pafA, katG, recR, blaR, Mab_1456c) and tested the persistence phenotype of these strains. Rather surprisingly only 2 of the 5 hits (katG and pafA) exhibited a significant persistence defect when compared to wild type upon exposure to TIG/LZD and this was complemented using an integrative construct. The authors then investigated the specificity of delta-katG susceptibility against different antibiotic classes and demonstrated increased killing by rifabutin. The katG phenotype was shown to be mediated through the production of oxidative stress which was reverted when the bacterial cells were cultured under hypoxic conditions. Interestingly, when testing the role of katG in other clinical strains of Mab, the phenotype was observed only in one of the clinical strains demonstrating that there might be alternative anti-oxidative stress defense mechanisms operating in some clinical strains.

Strengths:

While the role of ROS in antibiotic mediated killing of mycobacterial cells have been studied to some extent, this paper presents some new findings with regards to genetic analysis of M. abscessus susceptibility, especially against clinically used antibiotics, which makes it useful. Also, the attempts to validate their observations in clinical isolates is appreciated.

Weaknesses:

Amongst the 5 shortlisted candidates from the screen, only 2 showed marginal phenotypes which limits the impact of the screening approach.

We appreciate the reviewer’s comments, but we note that 4 out of 5 genes displayed phenotypes concordant with findings of the Tn-Seq data, with katG and pafA, as well as MAB_1456c (during starvation only) and blaR (in rich media only) having decreased survival as shown in Figure 3A-D. We do agree that some of the phenotypes were more modest in a single-mutant context than in the pooled Tn-Seq screen. In addition, several mutants that had modest changes in survival also showed profound defects in resuming growth after removal of antibiotics, with the pafA mutants particularly impaired. (Figure 3 - figure supplement 1).

While the role of KatG mediated detoxification of ROS and involvement of ROS in antibiotic killing was well demonstrated, the lack of replication of this phenotype in some of the clinical isolates limits the significance of these findings.

While the role of katG varied among strains, the antibiotic-induced accumulation of ROS was seen in all three strains (Figure 6A). This suggests that in some strains other ROS-detoxification pathways are able to compensate for the loss of katG.

(Figure 2—figure supplements 1–3)

Figure 1—figure supplement 1.

Reviewer #2 (Public review):

Summary:

The work set out to better understand the phenomenon of antibiotic persistence in mycobacteria. Three new observations are made using the pathogenic Mycobacterium abscessus as an experimental system: phenotypic tolerance involves suppression of ROS, protein synthesis inhibitors can be lethal for this bacterium, and levofloxacin lethality is unaffected by deletion of catalase, suggesting that this quinolone does not kill via ROS.

Strengths:

The ROS experiments are supported in three ways: measurement of ROS by a fluorescent probe, deletion of catalase increases lethality of selected antibiotics, and a hypoxia model suppresses antibiotic lethality. A variety of antibiotics are examined, and transposon mutagenesis identifies several genes involved in phenotypic tolerance, including one that encodes catalase. The methods are adequate for making these statements.

Weaknesses:

The work can be improved by a more comprehensive treatment of prior work, especially comparison of E. coli work with mycobacterial studies.

Moreover, the work still has some technical issues to fix regarding description of the methods, supplementary material, and reference formating.

See detailed responses below.

Overall impact: Showing that ROS accumulation is suppressed during phenotypic tolerance, while expected, adds to the examples of the protective effects of low ROS levels. Moreover, the work, along with a few others, extends the idea of antibiotic involvement with ROS to mycobacteria. These are fieldsolidifying observations.

Comments on revisions:

The authors have moved this paper along nicely. I have a few general thoughts.

It would be helpful to have more references to specific figures and panels listed in the text to make reading easier.

Text modified to add more figure references.

(1) I would suggest adding a statement about the importance of the work. From my perspective, the work shows the general nature of many statements derived from work with E. coli. This is important. The abstract says this overall, but a final sentence in the abstract would make it clear to all readers.

We appreciate the suggestion and have added a line to the abstract.

(2) The paper describes properties that may be peculiar to mycobacteria. If the authors agree, I would suggest some stress on the differences from E. coli. Also, I would place more stress on novel findings. This might be done in a section called Concluding Remarks. The paper by Shee 2022 AAC could be helpful in phrasing general properties.

We have added mention of this in the discussion (lines 354-356).

(3) Several aspects still need work to be of publication quality. Examples are the materials table and the presentation of supplementary material. Reference formatting also needs attention.

We respond to the specific details below.

Reviewer #3 (Public review):

Summary:

The manuscript demonstrates that starvation induces persister formation in M. abscesses.

They also utilized Tn-Seq for the identification of genes involved in persistence. They identified the role of catalase-peroxidase KatG in preventing death from translation inhibitors Tigecycline and Linezolid. They further demonstrated that a combination of these translation inhibitors leads to the generation of ROS in PBS-starved cells.

Strengths:

The authors used high-throughput genomics-based methods for identification of genes playing a role in persistence.

Weaknesses:

The findings could not be validated in clinical strains.

Comments on revisions: No more comments for the authors.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The authors are strongly encouraged to check the references. There is some systematic error in the citations of references. Started to list but then they were too many.

For example Ln 51, Ref #11 cited, should be #10. Ln 59, #18 is wrongly cited. Should be - Ln 104. Ref #27 wrongly cited.

Ref #26 and #28 identical.

Even in discussion section a lot of references are mis-cited.

We very much appreciate the reviewer catching this issue with the import of our references and we have corrected this.

Reviewer #2 (Recommendations for the authors):

Below I have listed comments on specific issues that I hope are useful during revision.

Line 21 population is singular

Text modified

Line 21 comma after antibiotic (subordinate clause) Line

Text modified

25 is how singular?

Text modified

Impression of abstract: the work seems to confirm and therefore generalize concepts derived from studies with E. coli. If the authors agree, such a statement would be appropriate as a final sentence. I would also look for novel features to stress in the abstract.

Line 41 this challenge is vague

Text modified

Line 43 comma such as (also comma at the end of the parenthetical statement). This type of comma error is common throughout the manuscript and slows reading.

Text modified

Line 60 paradoxically. Is this the best concept? Or is it the natural effect of evolution (assuming that mycobacteria or their ancestors were exposed to environmental antibiotics)?

It is certainly problematic for clearing infection.

Text not modified.

Line 63 highlighted uncertainties ... meaning is unclear especially since you may have changed what "model" is referring to.

Text modified

Line 66 models.... Do you really mean systems? Models of what?

This refers to mechanistic models. Text not modified.

Line 67 arrest cell division. This is written as if it were true. Does the evidence point specifically to cell division or perhaps more accurately suppression of metabolism (see Ye et al 2025 mBio).

Both have been postulated as important. Text modified to add concept of metabolism

... targeted by antibiotics non-essential... Do you think that antibiotics work by inactivating essential targets? That seems overly simplistic, as lethal action is more likely the metabolic response to the damage caused. By the end of the paragraph you come around to this view, but you have already misdirected the reader. The reader is not sure what to believe. Line 70 note that there are many inhibitors of transcription and translation that only block growth, they do not rapidly kill cells

There can be both direct, and indirect secondary killing mechanisms. We devote a significant portion of the Discussion section to this topic.

Line 71 debate. There was indeed a debate, but reference 22 is not a valid citation for this. I think you mislead the reader by not accurately describing the debate. It was basically about the inability of Kim Lewis and James Imlay to reproduce the work of ref. 22. A great deal of prior work and then subsequent work showed that the challenge to ref. 22 lacked substance.

(1) Text modified to fix an error in the citation number related to direct β-lactam-mediated lysis.

(2) We agree that there is a great deal of data supporting antibiotic-induced ROS as important for bactericidal activity in many circumstances and do not argue otherwise. This sentence points out that over the years the paradigm for how antibiotics kill bacteria has evolved.

Line 80. It seems you are starting a new topic here. What about beginning a new paragraph?

The paragraph introduces mycobacteria of which Mabs is one. Text not modified.

Line 85 delete the comma: it implies a compound sentence that is not delivered.

Text modified.

Line 109 screen singular

Text modified.

Line 156 these conditions is imprecise and vague

Conditions were described in paragraph above in the manuscript. Text not modified.

Fig 2 it would be helpful to more clearly define the meaning of the coordinates

Text modified.

Line 230 and throughout please indicate the location of the data being cited for rapid reader reference

Text modified.

Lines 315-323 You could use this paragraph as the first of the Discussion. Some readers prefer to read the Discussion before the results. For them, a summary at the beginning of the Discussion is useful.

Text modified.

Line 328 without underlying mechanism... for E. coli refer to Zeng PNAS 2022. Depending on when the final version of this paper happens, there should be a figure in a Zhao Zhu mLife paper on purA that will have been published. Since it is not yet available, it cannot be cited.

We agree that the Zeng et al study is interesting and have added this reference to our discussion. However, these findings related to broad Crp-regulated tolerance actually underscore the point that we are making: that there are multiple factors (Crp, RelA, Lon, TisB, MazE, others) that mediate antibiotic tolerance.

Line 339 where are the data?

These data are in Figure 5, panels C, D. We have clarified the text to indicate that only a single agent from each of these classes was tested.

Line 346 here you are summarizing evidence for ROS in killing mycobacteria. You should include the moxifloxacin study by Shee et al 2022 AAC.

Reference added.

Line 348 refer to James Collins' work with E. coli in which his lab examined agents with a variety of mechanisms. There seems to be a fundamental difference between E. coli and mycobacteria with respect to rifampicin, a strictly static agent in E. coli but clearly lethal in mycobacteria. Note that chloramphenicol is static in E. coli and blocks ROS production. What does it do in mycobacteria? A brief discussion of this difference might be relevant at line 362

Text modified.

Lines 364-368 Here the idea might be simply that there are two modes of killing, one that is a direct extension of class-specific damage (chromosome fragmentation with fluoroquinolones, for example, or cell lysis by beta-lactams) and a second that is a metabolic response to the antibiotic damage (ROS accumulation). The second type is not class specific. Within this context, the mycobacterial killing by rifampicin might be a class-specific extension of inhibition of transcription that does not occur in E. coli.

Agreed, text modified to include this.

Line 400 The Key Resource table is not of publication quality. Precision and repeatability can be improved by spelling out the name of the vendor and its location (City, Country). In the present case, use of BD is lab jargon.

We appreciate the reviewer’s precision. However, this is actually not lab jargon. Becton, Dickinson and Company now refers to itself as BD (see https://www.bd.com/en-us), and the American Type Culture Collection now refers to itself as ATCC (see https://www.atcc.org/about-us/who-we-are).

Line 639 It would be good to have experienced colleagues critically review the manuscript, especially for English usage. Listing those persons here adds to the credibility of the work

Text not changed.

References: please refer to the journal style. Here you use italic for titles and scientific names, thereby obscuring the scientific names. Normally article titles are not italic and scientific names are ALWAYS italic unless prohibited by journal style.

Our reference format is concordant with eLife submission guidelines, and all references are reformatted by the journal at the time of final publication (see https://elifesciences.org/insideelife/a43f95ca/elife-references-yes-we-take-any-format-no-we-re-not-rekeying).

Supplemental Material: Please refer to journal style. Normally this is a stand-alone document that includes a title page and carefully crafted figure legends. Supplemental figures would be numbered as 1, 2, ... A professional appearing Supplemental Material section shows author publication experience not obvious in other parts of the paper. The text indicated MIC determinations. I would like to see a table of MIC values.

(1) MIC table added as Supplemental Table 5.

(2) The Supplemental figures are submitted and named in accordance with eLife instructions. Please note that for eLife, there is not a stand-alone supplementary figure section with a title page as you are requesting, but instead the figure supplements for each figure are provided as online files linked to each figure.

Author response:

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

Public Reviews:

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.

We appreciate the Reviewer’s consideration of the strengths of our study supporting the identification of adult endothelial to hematopoietic transition (EHT) in the mouse bone marrow.

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.

Recognizing the importance of the weaknesses pointed by the Reviewer, we provide below our response to the thoughtful recommendations rendered.

Reviewer #1 (Recommendations for the authors):

The main model is to label cells using Cdh5 (VE-cadherin) CreERT2 genetic tracing. Cdh5 is a typical marker of endothelial cells. The data shows that, when treating adults with tamoxifen, the model labels PBMCs after ~10 days, and the labeling kinetics plateau by day 14... The authors reach the main conclusion: that adult ECs are making hematopoietic cells.

We agree that the main tool used in this study is to label endothelial cells (ECs) using Cdh5 (VE-Cadherin) CreERT2 genetic tracing in mice. Indeed, Cdh5 is recognized as a good marker of ECs. As a minor point, we wish to clarify that the results from treating adult Cdh5-CreERT2 mice with tamoxifen (Figure 1F) show that the ZsGreen labeling kinetics plateau by day 28 (not by day 14).

Important controls should be shown to rule out alternative possibilities: namely, that the CreERT2 reporter is being sparsely expressed in HSPCs. Many markers, specific as they may seem to be, can show expression in non-specific lineages - particularly in the cases of BAC and PAC transgenic models, in which the transgene can be present in multiple tandem copies and subject to genome location-specific effects. As the authors remind readers, the Cdh5 gene is partly transcribed (though at low levels) in HSPCs, and even more clearly expressed in specific subpopulations such as CLPs, DCs, pDCs, B cells, etc. Some options would be to: i) check if the Cdh5-CreERT2 transgene (not endogenous Cdh5, but the BAC/PAC transgene) is expressed in LSKs (at least by qPCR), ii) verify if any CreERT2 protein levels are present in LSKs (e.g., by western blot), and iii) check if tamoxifen is labeling any HSPCs freshly after induction (e.g., flow cytometry data of ZsGreen LSKs at 24-48h post tamoxifen injection).

We fully agree with the Reviewer that many markers, allegedly specific to a certain cell type, can show expression in other cell lineages. We also agree that excluding sparse or ectopic CreERT2 expression in hematopoietic stem and progenitor cells (HSPCs) is essential for interpreting lineage-tracing results. As suggested by the Reviewer, we have now examined if the Cdh5-CreERT2 transgene is expressed in bone marrow LSKs. To this end, we analyzed the Polylox single-cell RNAseq dataset presented in this study, containing ZsGreen⁺ ECs and enriched ZsGreen⁺ LSKs. As shown in the revised Figure S4D, CreERT2 transcripts were detected exclusively in Cdh5-expressing endothelial populations and were absent from Ptprc/CD45-expressing hematopoietic cells, except for plasmacytoid dendritic cells (pDCs; Figure S4E). These results are consistent with the RNAseq data from adult mouse bone marrow[1] showing that the Cdh5 gene is not expressed in HSPCs, CLPs, DCs, or B cells. Rather, among hematopoietic CD45⁺ cells, Cdh5 is only expressed in a small subset of plasmacytoid dendritic cells (pDCs), which are terminally differentiated cells. These published results are described in the text.

To further support this conclusion, we provide additional single-cell RNAseq analyses from our unpublished dataset of LSKs isolated from Cdh5-CreERT2/ZsGreen mice and not enriched for ZsGreen expression. These new analyses were performed after integrating the single-cell data from ECs and ZsGreen⁺ hematopoietic cells from the Polylox dataset (current study). As shown in Author response images 1 and 2, CreERT2 expression closely matches the expression patterns of Cdh5, Pecam1, and Emcn and is not detected in Ptprc/CD45-expressing hematopoietic cells.

Author response image 1.

Expression of CreERT2, Cdh5, Ptprc and ZsGreen in BM cell populations enriched with ECs and hematopoietic cells. The single-cell RNAseq results are derived from ZsGreen-enriched BM ECs and ZsGreen-enriched BM hematopoietic cells were derived from Polylox lineage-tracing experiments (data shown in Fig. 5; 37,667 ECs and 48,065 BM hematopoietic cells) and from LSKs (23,017 cells) independently isolated from tamoxifen-treated Cdh5-CreERT2/ZsGreen mice without ZsGreen enrichment (unpublished data).

Author response image 2.

Expression of CreERT2, Cdh5, Ptprc, Pecam1, Emcn, ZsGreen1, Col1a2, Cd19, Cd3e, Itgam (CD11b), Ly6a (Sca-1), Kit(cKit), Cd34, Cd48, Slamf1 (CD150), and Siglech in enriched BM ECs and LSKs from Cdh5-CreERT2/ZsGreen mice treated with tamoxifen 4 weeks prior to harvest (same cell source as indicated in Author response image 1).

Additionally, we functionally tested whether hematopoietic progenitors could acquire ZsGreen labeling following tamoxifen administration using transplantation assays (Figure 4A-D). ZsGreen^- LSKs (purity 99%), sorted from Cdh5-CreERT2/ZsGreen donors that had never been exposed to tamoxifen to exclude background Cre leakiness, were transplanted into lethally irradiated wild-type recipients. After stable hematopoietic reconstitution, recipients were treated with tamoxifen. If transplanted HSPCs or their progeny expressed CreERT2, tamoxifen administration would be expected to induce ZsGreen labeling. However, no ZsGreen⁺ hematopoietic cells were detected in these recipients, demonstrating that hematopoietic progenitors from Cdh5-CreERT2/ZsGreen and their descendants do not undergo tamoxifen-induced recombination.

Together, the single-cell transcriptional and transplantation data demonstrate that CreERT2 expression and tamoxifen-induced recombination are restricted to Cdh5-expressing ECs (except for pDCs). These findings support the conclusion that ZsGreen⁺ hematopoietic cells arise from adult bone marrow ECs rather than from contaminating hematopoietic progenitors.

One important missing experiment is to trace how ECs actually do this hematopoietic conversion: meaning, which populations of HSPCs are being produced by adult ECs in the first instance? LT-HSCs? ST-HSCs? MPPs? GMPs? All of the above? What are the kinetics? Differentiation is likely to follow a hierarchical path, but this is unclear at the moment.

We agree that defining the earliest EC-derived hematopoietic cell progenitors and the kinetics by which these progenitors appear (LT-HSC vs ST-HSC/MPP vs lineage-restricted progenitors) would provide important insights into adult EHT.

In the current genetic labeling system, a rigorous kinetic analysis of hematopoietic cells first generated by EC-derived in vivo is not straightforward. Specifically, the low-level baseline reporter ZsGreen⁺ fluorescence in hematopoietic cells (dependent on EHT occurring prenatally, perinatally or in young mice or other causes (Figure 1 A-D and Figure S1 D-I) impairs identification of newly generated ZsGreen⁺ progenitors at early time points and distinguish them from baseline fluorescence. A potential solution might be to introduce serial harvests across multiple time-points in large mouse cohorts to capture rare transitional events with statistical significance.

We wish to emphasize that the primary objective of this study was to establish whether adult bone marrow ECs have a hemogenic potential. Our data demonstrate adult EC-derived hematopoietic cell output that includes progenitor-containing fractions and multilineage mature progeny, under both steady-state conditions. We acknowledge that the current work does not resolve the order and kinetics of hematopoietic cell emergence following EHT. Therefore, under “Limitations of the study” we explicitly state this limitation and frame the identification of the earliest endothelial-derived progenitors and their kinetics as an important direction for future work.

One warning sign is how rare the reported phenomenon is. Even when labeling almost 90% of the BM ECs, these make at most ~3% of blood (less than 1% in the transplants in Figure 4F, less than 0.5% in the col1a2 tracing in Figure 7). This means this is a very rare and/or transient phenomenon... The most major warning sign is the fast kinetics of labeling and the fast plateau. We know that: a) differentiation typically follows some hierarchy, b) in situ dynamics of blood production are slow (work by Rodewald and Höfer). Considering how fast these populations need to be replaced to reach a steady state so rapidly (as reported here, 2-4 weeks), the presumably specialized ECs would need to be steadily dividing and producing hematopoietic cells at a fast pace (as a side prediction, the adult "EHT" cluster would likely be highly Mki67+). More importantly, the ZsGreen LSKs produced by the ECs would have to undergo VERY rapid differentiation (much faster than normal LSKs) or otherwise, if 3% of them are produced by a top compartment (the BM ECs) every 4 weeks, then the labeled population would continue to grow with time. The authors could try to challenge this by testing if the ZsGreen LSKs undergo much faster differentiation kinetics or lower self-renewal (which does not seem to be the case, at least in their own transplantation data). We believe a more likely explanation is that the label is being acquired more or less non-specifically, directly across a bunch of HSPC populations.

The Reviewer correctly notes that that the population of hemogenic ECs in the adult mouse bone marrow is small and the output of hematopoietic cells from these hemogenic ECs accounts for at most 3% of blood cells. We agree that delineating the kinetics by which hematopoietic cells are generated from adult EC is important, as this information would provide important insights into adult EHT.

Nonetheless, we believe that the rapid appearance and early plateau of labeled blood cells in our experiments may not derive from a sustained, high-rate generation of labeled blood cells from self-renewing top-tier hematopoietic cell compartments, such as LT-HSCs. Rather, our data are more consistent with a predominantly lineage-restricted and biased hematopoietic progenitor cell population being the source of labeled blood cells. Supporting this interpretation, longitudinal analysis of peripheral blood shows that EGFP⁺ PBMCs are consistently enriched with myeloid cells, whereas EGFP^- PBMCs are predominantly B cells (Figure 4G and H). This myeloid lineage skewing is stable over time and contrasts with what would be expected if labeling were acquired broadly and nonspecifically across the hematopoietic hierarchy. Therefore, our results are more consistent with myeloid biased progenitors being among the first populations that EHT generates.

We acknowledge that our studies do not identify the earliest endothelial-derived hematopoietic cells produced in vivo, and do not define their differentiation kinetics. Addressing rigorously these questions would require temporally resolved lineage tracing with sufficiently powered cohorts at early time point to statistically distinguish from baseline reporter background. These important experiments were beyond the scope of the present study. As noted above, under “Limitations of the study” we explicitly state this limitation and frame the identification of the earliest endothelial-derived progenitors and their kinetics as an important direction for future work.

Transplant experiments in Figure 4 do offer a crucial experiment in support of the main conclusion of the manuscript. These experiments show that transplanted LSKs bearing the Cdh5-CreERT2 and ZsGreen reporter cannot acquire the tamoxifen-induced label post-transplantation - suggesting that the label is coming from ECs. However, it is also possible that the LSK Cdh5-CreERT expression is partly during the transplantation process... Indeed, we know through the aging data that the labeling is less active in aged mice. In any case, this would be verified by qPCR/western-blot (comparing native vs post-transplant LSKs).

We agree with the Reviewer that the experiment in Figure 4A-D “offer a crucial experiment in support of the main conclusion of the manuscript.” The results of this experiment show that ZsGreen negative LSKs from the Cdh5-CreERT2-ZsGreen reporter mice do not acquire tamoxifen-induced ZsGreen fluorescence post transplantation, supporting the endothelial cell origin of blood ZsGreen⁺cells.

The Reviewer raises the possibility a “that the LSK Cdh5-CreERT expression is partly during the transplantation process... , and that this Cdh5-CreERT expression may occur slowly as learned “through the aging data that the labeling is less active in aged mice.” As we show in Figure 3F, tamoxifen administration induced a similar percentage of ZsGreen⁺ECs in the bone marrow of Cdh5-Cre^ERT2(BAC)/ZsGreen mice, whether tamoxifen was administered to 6-week-old, 16-week-old, 26-week-old or 36-week-old mice. Similar results with Cdh5-CreERT2 (BAC) mice are reported in the literature[2]. Since the mice transplanted with ZsGreen^- LSKs were followed for 25 weeks after tamoxifen administration, we believe that the results in Figure 4A-D address the concern raised by the Reviewer.

Supporting the conclusion that LSKs from the Cdh5-CreERT2-ZsGreen reporter mice do not express the Cdh5-CreERT2 under a native -non-transplant- setting, we now provide transcriptomic data from Cdh5-CreERT2/ZsGreen mice (not transplanted) showing that CreERT2 expression closely tracks with expression of canonical endothelial markers (Cdh5, Pecam1, Emcn) and is not detectable in Ptprc/CD45-expressing hematopoietic cells (Author response images 1 and 2). These data were obtained from non-transplanted mice treated with tamoxifen at ~12 weeks of age and analyzed four weeks later. Together, these results indicate that CreERT2 expression is endothelial-restricted in Cdh5-CreERT2-ZsGreen reporter mice.

Figure 5 presents PolyLox experiments to challenge whether adult ECs produce hematopoietic cells through in situ barcoding. Several important details of the experiment are missing in the main text (how many cells were labeled, at which time point, how long after induction were the cells sampled, how many bones/BM-cells were used for the sample preparation, what was the sampling rate per population after sorting, how many total barcodes were detected per population, how many were discarded/kept, what was the clone-size/abundance per compartment). As presented, the authors imply that 31 out of ~200 EC barcodes are shared with hematopoietic cells... This would suggest that ~15% of endothelial cells are producing hematopoietic cells at steady state. This does not align well with the rarity of the behavior and the steady state kinetics (unless any BM EC could stochastically produce hematopoietic cells every couple of weeks, or if the clonality of the BM EC compartment would be drastically reduced during the pulse-chase overlap with mesenchymal cells. Important controls are missing, such as what would be the overlap with a population that is known to be phylogenetically unrelated (e.g., how many of these barcodes would be found by random chance at this same Pgen cut-off in a second induced mouse). Also, the Pgen value could be plotted directly to see whether the clones with more overlapping populations/cells (3HG, 127, 125, CBA) also have a higher Pgen. We posit that there are large numbers of hematopoietic clones that contribute to adult hematopoiesis (anywhere from 2,000-20,000 clones would be producing granulocytes after 16 weeks post chase), and it would be easy to find clones that overlap with granulocytes (the most abundant and easily sampled population) - HSPCs would be the more stringent metric.

We thank the Reviewer for highlighting the need for a more detailed description of the Polylox experiments. To address this deficiency, we have compiled a document (Additional Supplementary Information file) containing all the specifics of the Polylox experimental and analytical parameters in one location. This includes: (i) the number of cells analyzed per population, (ii) the time points of induction and sample collection, (iii) the number of bones and total bone marrow cells used for preparation, (iv) the sampling rate following cell sorting, (v) the total number of detected barcodes per population, (vi) barcode filtering criteria and numbers retained or discarded, and (vii) clone-size and barcode number across cell compartments. We have updated the manuscript to refer readers to this Supplementary file.

The Reviewer concluded from our results (Figure 5, Figure S5) that 31 out of ~200 endothelial cell (EC) barcodes shared with hematopoietic cells (HCs), implying that ~15% of ECs produce hematopoietic cell progeny at steady state. This interpretation in inconsistent with our data showing the rare nature of adult EHT and would require either that a large fraction of bone-marrow ECs can generate hematopoietic cells within short time windows, or that EC would clonally expand rapidly during the pulse-chase period, as noted by the Reviewer. The explanation for this apparent problem is technical. Briefly, the ~200 EC barcodes recovered do not represent all barcoded ECs. During Polylox barcode library construction, a mandatory size-selection step is applied prior to PacBio sequencing, retaining fragments that are approximately 800–1500 bp in length, whereas the full Polylox cassette spans ~2800 bp. This is mainly because the PacBio sequencer requires that the library be either 800-1500bp or over 2500bp, for optimal sequencing results. As described in the original Polylox publication[3,4], this size selection eliminates most (approximately 75%) longer barcodes, together with ~85% of the shorter barcodes. Thus, ECs harboring very long or short recombined barcodes are under-represented or excluded from sequencing. As a result, the 22 true barcodes linking ECs and HCs recovered from sequencing do not indicate that ~10–15% of ECs generate hematopoietic progeny. Rather, these barcodes represent a highly selected subset of ECs with barcode configurations compatible with library recovery and sequencing. The observed EC–HC barcode sharing thus reflects qualitative lineage connectivity, not the quantitative frequency of endothelial-derived hematopoiesis at steady state.

The Reviewer correctly notes that true Polylox barcodes are shared by ECs and mesenchymal-type cells and asks that we examine whether this overlap could occur by chance alone. The Polylox filtering threshold (pGen < 1 × 10^-6), that we have revised for stringency (from pGen < 1 × 10^-4, without altering the essential results; new Figure S4 and revised Figure 5C-F) renders such overlap exceedingly unlikely. At this threshold, the expected number of random recombination events among 4,069 barcoded cells is approximately 0.004. Consequently, among the 87 mesenchymal cells identified here, fewer than 0.4 cells would be expected, to share a barcode with another cell by chance alone. Thus, the probability of recovering identical barcodes across unrelated lineages due to random recombination is vanishingly small, and the observed EC–mesenchymal barcode sharing substantially exceeds random expectation.

Related to this observation, the Reviewer correctly notes that the endothelial and mesenchymal cell lineages are phylogenetically unrelated. However, endothelial-to-mesenchymal cell transition (EndMT), the process by which normal ECs completely or partially lose their endothelial identity and acquire expression of mesenchymal markers, is a well-established process that occurs physiologically and in disease states (Simons M Curr Opin Physiol 2023). In the bone marrow, the occurrence of EndMT has been documented in patients with myelofibrosis, and the process affects the bone marrow microvasculature (Erba BG et al The Amer J Patholl 2017). Single-cell RNAseq of non-hematopoietic bone marrow cells has shown the existence of a rare population of ECs that co-expresses endothelial cell markers (Cdh5, Kdr, Emcm and others) and the mesenchymal cell markers, as shown in Figure 6E and F.

We fully agree with the Reviewer that given the large number of hematopoietic clones contributing to adult hematopoiesis -particularly granulocyte-producing clones- it may be relatively easy to detect barcode overlap with abundant mature populations, whereas overlap with HSPCs would represent a more stringent and informative metric of lineage relationships. The Polylox results presented here show the sharing of true barcodes between individual ECs and HSPC.

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.

We thank the Reviewer for the supportive comments about our study.

(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.

We agree that FACS sorting can never achieve 100% cell purity and that sorting purity is critical for interpreting the ex vivo culture experiments presented in our study. As requested by the Reviewer, we have now documented the purity of the sorted endothelial cell (EC) population used in the ex vivo culture experiments. The post-sort purity of CD45<sup->/sup>VE-cadherin⁺ZsGreen⁺ ECs was 96.5 %; this data is now shown in the revised Figure 2B (Post Sort Purity panel). This purity level is comparable to purity levels of sorted ECs shown in Figure S2I (94.5 %).

While we agree that a detailed time-course analysis of hematopoietic cell output from EC cultures could further strengthen the conclusion that bone marrow ECs can produce hematopoietic cells ex vivo, we wish to call attention to the additional critical control in the experiment shown in Figure 2B-D. In this experiment, we co-cultured CD45⁺ZsGreen⁺ hematopoietic cells from Cdh5-CreERT2/ZsGreen mice, rather than ECs, and examined if these hematopoietic cells could produce ZsGreen⁺ cell progeny after 8-week culture under the same conditions used in EC co-cultures (conditions not designed to support hematopoietic cells long-term). Unlike ECs, the CD45⁺ZsGreen⁺ hematopoietic cells did not generate ZsGreen⁺ hematopoietic cells at the end of the 8-week culture, indicating that the culture conditions are not permissive for the maintenance, proliferation and differentiation of hematopoietic cells. This provides strong evidence that even if few hematopoietic cells contaminated the sorted ECs, these hematopoietic cells would not contribute to EC-derived production of hematopoietic cells at the 8-week time-point. We have revised the text of the results describing the results of Figure 2B-D.

(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.

The original manuscript reported survival and engraftment up to 12 weeks post transplantation. The recipient mice have now been monitored for up to 10 months post transplantation. These extended survival and engraftment data are now included in the revised Figure 2I and J replacing the previous 10-week analyses.

We agree with the Reviewer that the time-course kinetics of donor cell repopulation would help define adult endothelial to hematopoietic transition (EHT) and the hematopoietic cell types produced by adult (EHT). We did not perform serial time-course sampling of peripheral blood beyond the 10-week and the 10-month time-points. Given that the recipient mice were lethally irradiated with increased susceptibility to infection, we sought to minimize repeated interventions that could compromise animal health and survival. We therefore prioritized long-term survival and endpoint analysis over repeated longitudinal sampling. Nonetheless, the long-term survival,10 months, and multilineage hematopoietic cell reconstitution after lethal irradiation provides functional evidence that adult EHT produced at least some LT-HSC.

We acknowledge that phenotypic assessment of bone marrow LT-HSC chimerism /or secondary transplantation would further strengthen the manuscript. We have clarified these limitations in the revised manuscript under “Limitations of the study”.

(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.

We agree with the Reviewer that, in most cases, a larger number of experimental data points is helpful to strengthen the conclusions, and that having additional mice transplanted with ZsGreen-enriched LSK would be desirable. However, we do not believe that additional mice transplanted with ZsGreen LSKs would strengthen the conclusions drawn from the experimental results shown in Figure 4D, in which we used 6 mice transplanted with ZsGreen-depleted (ZsGreen^-) LSKs and 2 mice transplanted with ZsGreen⁺-enriched (ZsGreen⁺) LSKs. The independence of adult EHT from “pre-existing hematopoietic cell progenitors” is based on the following experimental results and conclusion from these results.

First, ZsGreen^- LSKs (purity 99%) isolated from Cdh5-CreERT2/ZsGreen mice were transplanted into lethally irradiated WT recipients (n = 6). These ZsGreen^- LSKs robustly reconstituted hematopoiesis, demonstrating successful engraftment. Importantly, tamoxifen administration to the recipients of ZsGreen^- LSKs produced no detectable ZsGreen⁺ cells in the blood for up to 6 months post transplantation (Figure 4D, blue line encompassing the results of the 6 mice). This result demonstrates that the transplanted ZsGreen^- hematopoietic progenitors and their progeny do not acquire ZsGreen labeling in vivo following tamoxifen treatment, indicating that they lack the Cre-recombinase. This result is consistent with the endothelial specificity of Cdh5 expression.

Second, ZsGreen⁺ LSKs (accounting for ~50% of the LSKs) isolated from Cdh5-CreERT2/ZsGreen mice were transplanted into lethally irradiated WT recipients (n = 2). This arm of the experiment was performed in part as a technical control to confirm successful engraftment and detection of ZsGreen⁺ hematopoietic cells in the transplant setting. Importantly, tamoxifen administration to the two recipients of ZsGreen⁺ LSKs (Figure 4D, two green lines reflecting these two mice) show that the level of ZsGreen⁺ blood cells stabilized in each of the mice between week 10 and 24, showing equilibrium between the proportion of ZsGreen⁺ and ZsGreen^-cells in the blood. This indicates that pre-existing ZsGreen⁺ LSK are not responsible for tamoxifen-induced increases in ZsGreen⁺ hematopoietic cell in blood.

Together, the results from this experiment demonstrate that in the setting of transplantation, tamoxifen does not induce ZsGreen labeling of ZsGreen- hematopoietic progenitors/their progeny. This result strongly supports the conclusion that ZsGreen⁺ hematopoietic cells arise independently of pre-existing or inducible hematopoietic progenitors. We have revised the text to clarify these experiments and to present the results in a simplified manner.

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.

We agree that the biological significance and functional roles of hematopoietic cells generated de novo from adult bone marrow ECs remain important open questions. We also agree that the output of hematopoietic cells from adult EHT is low, but rare events can be important, particularly as they pertain to stem/progenitor cell biology. Both points are described under “Limitations of the study”. The primary goal of the present study was to address the question whether adult bone marrow ECs can undergo EHT. We believe that the combination of various mouse transgenic lines, different Cre-ER, different reporters (ZsGreen and mTmG), including the s.c. barcoding reporter (PolyloxExpress), different approaches to evaluate hematopoiesis in vivo and ex vivo, makes it rather unlikely that our conclusions are driven by an artifact related to a specific leaky reporter, contamination, or problems with one of the Cre-lines. The experiment where we find no tamoxifen-induced labeling of transplanted ZsGreen^- LSKs derived from the Cdh5-CreERT2/ZsGreen mice is strongly supportive of the existence of adult EHT, virtually excluding a contribution of contaminant hematopoietic cells.

Reviewer 2 Recommendations for the authors:

(1) There is a discrepancy in the proportion of peripheral blood composition between different reporters (mTmG and ZsGreen) (Figure 1G and Figure S1K), especially the contrasting B cell proportion between both models. The additional comments on this data should be mentioned.

In the revised Results section, we now note that the mTmG and ZsGreen reporters show slightly different efficiencies or kinetics of labeling. These differences have previously been reported[5] and have been attributed to relative reporter leakiness, sensitivity to tamoxifen, or different kinetics of Cre recombination. As suggested, these comments have been added to the text following the description of (Figure S2A).

(2) Experimental methods concerning cell transplantation/transfer need more information, such as: a) using or not using rescue cells and how many cells are they if using, b) single or split dose of irradiation, c) when were cells transplanted following irradiation, etc. Otherwise, the data are uninterpretable.

We have ensured that the Material and Methods section under “Bone marrow ablation and transplantation” contains all the information requested by the Reviewer.

(3) Some of the grouped data haven't been statistically analyzed.

We have reviewed all data and performed appropriate statistical analyses where comparisons were made. In the revised figures and legends, all grouped datasets now include statistical tests and p-values are indicated (added to Fig. 3H and I; Figure 4G).

(4) Some flowcytometry plot has the quantitative number, others do not. The quantitative information is absolutely needed in all flow cytometry plots.

We have updated the flow cytometry figures to include quantitative values (percentages or absolute counts) in all relevant plots (2B (new figure, bottom left); 2C; S1G, S1H).

(5) It is more relevant to present the Emcn/VE-Cadherin plot from gated CD45+/ZsGreen+, not the CD45-/ZsGreen+ fraction (Figure 2C), as the latter were not the EHT-derived offspring, but rather the common phenotypic endothelial cells

As requested, we have added the suggested flow cytometry plot. The revised Figure 2C now includes an Emcn vs. VE-Cadherin plot from the gated CD45⁺ZsGreen⁺ population. This complements the existing panel and confirms that the cells of interest retain endothelial cell markers after culture, while the CD45⁺ZsGreen⁺ cells did not express endothelial markers. The figure legend has been updated to explain the new panel. We agree that this plot more directly highlights the phenotype of the presumed EHT-derived cells.

(6) To show the effect of the ex vivo culture, the authors should present the absolute number of CD45+ZsGreen+ cells in the pre-/post-culture; otherwise, the data are uninterpretable (Figure 2D).

Our interpretation of the Reviewer’s comment above (relative to the experiment shown in Figure 2B-D) is that the Reviewer would like that we provide the absolute number of CD45⁺ZsGreen⁺ cells introduced into the co-culture (supplemented with unsorted BM cells, ZsGreen⁺ hematopoietic cell or ZsGreen⁺ ECs) and the absolute number of CD45⁺ZsGreen⁺ cells recovered at the end of the 8-week culture. Currently, the results in Figure 2D show the absolute number of CD45⁺ZsGreen⁺ cells recovered at the end of the 8-week culture. The input of CD45⁺ZsGreen⁺ cells for unsorted BM cells was 2.93e6 on average; for ZsGreen⁺ hematopoietic cells was 1.68e6 on average and from sorted ZsGreen⁺ ECs was estimate up to 100.

(7) It is confusing to see Figures 2F and 2G, which apparently show the data from the middle of the experimental procedure (Figure 2E). Those data should be labelled clearly regarding which procedures of the whole experiment protocol.

As correctly noted by the Reviewer, Figures 2F and 2G provide data that relate to the middle of the graphical representation of the experiment shown in Figure 2E. We see how this may be confusing.

Therefore, we have updated both the figure labeling and legend to explicitly indicate that Figure 2F and 2G provide the FACS sorting results for the cells used for transplantation. The revised legend now reads: “Representative flow cytometry plots of the non-adherent cell fraction after 8 weeks of co-culture (cells used for transplantation).”

References

(1) Kucinski, I., Campos, J., Barile, M., Severi, F., Bohin, N., Moreira, P.N., Allen, L., Lawson, H., Haltalli, M.L.R., Kinston, S.J., et al. (2024). A time- and single-cell-resolved model of murine bone marrow hematopoiesis. Cell Stem Cell 31, 244-259.e10. https://doi.org/10.1016/j.stem.2023.12.001.

(2) Identification of a clonally expanding haematopoietic compartment in bone marrow | The EMBO Journal | Springer Nature Link https://link.springer.com/article/10.1038/emboj.2012.308.

(3) Pei, W., Shang, F., Wang, X., Fanti, A.-K., Greco, A., Busch, K., Klapproth, K., Zhang, Q., Quedenau, C., Sauer, S., et al. (2020). Resolving Fates and Single-Cell Transcriptomes of Hematopoietic Stem Cell Clones by PolyloxExpress Barcoding. Cell Stem Cell 27, 383-395.e8. https://doi.org/10.1016/j.stem.2020.07.018.

(4) Pei, W., Feyerabend, T.B., Rössler, J., Wang, X., Postrach, D., Busch, K., Rode, I., Klapproth, K., Dietlein, N., Quedenau, C., et al. (2017). Polylox barcoding reveals haematopoietic stem cell fates realized in vivo. Nature 548, 456–460. https://doi.org/10.1038/nature23653.

(5) Álvarez-Aznar, A., Martínez-Corral, I., Daubel, N., Betsholtz, C., Mäkinen, T., and Gaengel, K. (2020). Tamoxifen-independent recombination of reporter genes limits lineage tracing and mosaic analysis using CreERT2 lines. Transgenic Res 29, 53–68. https://doi.org/10.1007/s11248-019-00177-8.

Author response:

The following is the authors’ response to the original reviews

eLife Assessment

This study provides useful insights into addressing the question of whether the prevalence of autoimmune disease could be driven by sex differences in the T cell receptor (TCR) repertoire, correlating with higher rates of autoimmune disease in females. The authors compare male and female TCR repertoires using bulk RNA sequencing, from sorted thymocyte subpopulations in pediatric and adult human thymuses; however, the results do not provide sufficient analytical rigor and incompletely support the central claims.

The statement in the editorial assessment that our study “does not provide sufficient analytical rigor” surprised us. TCR repertoire analysis is indeed a highly complex domain, both experimentally and computationally. We consider ourselves to be leading experts in this field and have invested a great deal of effort to ensure the rigor and reproducibility of every analytical step.

Specifically, our group has previously benchmarked and published validated methodologies for the following areas: (i) TCR repertoire generation (Barennes et al., Nat Biotechnol 2021), (ii) repertoire analysis (Six et al., Frontiers in Immunol, 2013; Chaara et al., Frontiers in Immunol, 2018; Ritvo et al., PNAS, 2018; Mhanna et al., Diabetes, 2021; Trück et al., eLife, 2021; Quiniou et al., eLife, 2023; Mhanna et al., Cell Rep Methods, 2024; Mhanna et al., Nat Rev Primers Methods, 2024), and (iii) the curation and quality control of public TCR databases (Jouannet et al., NAR Genomics and Bioinformatics 2025). The current study applies these optimized and peer-reviewed pipelines, along with additional internal quality controls that we have been implemented over the years, ensuring the highest possible analytical standards for TCR repertoire studies.

We therefore respectfully feel that the phrase “insufficient analytical rigor” does not accurately reflect the methodological robustness of our work. This perception is also in contrast to the comment made by one of the reviewers, who explicitly noted that “overall, the methodologies appear to be sound.”

We would therefore be grateful if, upon reviewing our detailed point-by-point responses, the editors could reconsider this statement and tone it down in the final editorial summary.

With regard to comment that our results “incompletely support the central claims”, we will leave it to the reader’s judgement. We believe that our work provides a robust and transparent basis for future research into TCR repertoire, autoimmunity, and women’s health.

Reviewer 1 (Public reviews):

Summary

The goal of this paper was to determine whether the T cell receptor (TCR) repertoire differs between a male and a female human. To address this, this group sequenced TCRs from doublepositive and single-positive thymocytes in male and female humans of various ages. Such an analysis on sorted thymocyte subsets has not been performed in the past. The only comparable dataset is a pediatric thymocyte dataset where total thymocytes were sorted.

They report on participant ages and sexes, but not on ethnicity, race, nor provide information about HLA typing of individuals. Though the experiments themselves are heroic, they do represent a relatively small sampling of diverse humans. They observed no differences in TCRbeta or TCRalpha usage, combinational diversity, or differences in the length of the CDR3 region, or amino acid usage in the CD3aa region between males or females. Though they observed some TCRbeta CD3aa sequence motifs that differed between males and females, these findings could not be replicated using an external dataset and therefore were not generalizable to the human population.

They also compared TCRbeta sequences against those identified in the past using computational approaches to recognize cancer-, bacterial-, viral-, or autoimmune-antigens. They found very little overlap of their sequences with these annotated sequences (depending on the individual, ranging from 0.82-3.58% of sequences). Within the sequences that were in overlap, they found that certain sequences against autoimmune or bacterial antigens were significantly over-represented in female versus male CD8 SP cells. Since no other comparable dataset is available, they could not conclude whether this is a finding that is generalizable to the human population.

Strengths:

This is a novel dataset. Overall, the methodologies appear to be sound. There was an attempt to replicate their findings in cases where an appropriate dataset was available. I agree that there are no gross differences in TCR diversity between males and females.

We appreciate the positive feedback from the reviewer regarding these points.

Weaknesses:

Overall, the sample size is small given that it is an outbred population. The cleaner experiment would have been to study the impact of sex in a number of inbred MHC I/II identical mouse strains or in humans with HLA-identical backgrounds.

We respectfully disagree with the reviewer’s statement. We firmly believe that the issue we are dealing with, namely sex-based differences in thymic TCR selection relevant to autoimmunity, should be investigated more thoroughly in the general human population than in inbred mouse models.

While inbred mouse strains, being MHC I/II identical, eliminate the complexity of MHC variation, this comes at the cost of biological relevance. Firstly, a discrepancy in TCR generation or selection may only become apparent under specific MHC contexts, which could easily be overlooked when studying a single inbred strain. Secondly, inbred strains frequently contain fixed genetic variants that may influence thymic selection or immune regulation. This has the potential to introduce confounding effects rather than reducing them and not solving the generalization issue.

We are in full agreement that an HLA-matched human cohort would reduce inter-individual variability. However, such sampling is impossible in practice, as our thymic tissues were obtained from deceased organ donors, a collection effort that was, as the reviewer rightly noted, “heroic”. Despite these inherent limitations, the patterns we observed were consistent across multiple analytical approaches, lending robustness to our findings.

We now explicitly acknowledge this limitation in the Discussion of the revised manuscript and explain why, despite this constraint, our study provides meaningful and biologically relevant insights into human TCR selection and sex-related immune differences.

It is unclear whether there was consensus between the three databases they used regarding the antigens recognized by the TCR sequences. Given the very low overlap between the TCR sequences identified in these databases and their dataset, and the lack of replication, they should tone down their excitement about the CD8 T cell sequences recognizing autoimmune and bacterial antigens being over-represented in females.

The three databases used in this study - McPAS-TCR, IEDB, and VDJdb - provide complementary and partially non-overlapping specificity landscapes. McPAS-TCR is enriched for pathology-associated TCRs, while IEDB and VDJdb contain a higher proportion of viral specificities. Combining them therefore broadens the antigenic spectrum accessible for analysis and represents the most comprehensive approach currently possible to capture the diversity of TCR–antigen annotations.

With regard to the limited overlap between our dataset and these databases, this observation should be interpreted with caution. While the overlap may appear minimal at first glance, it is a biologically significant phenomenon. The public databases collectively contain only a minute fraction of the total universe of TCR specificities, estimated to exceed 10^15-21 possible receptors in humans. In this context, the observation of any overlap at all, particularly with coherent biological patterns such as the overrepresentation of autoimmune- and bacterialassociated TCRs in females, is noteworthy.

We have included a short clarification in the Discussion of the revised manuscript to make this point explicit and to further temper the language describing this finding.

The dataset could be valuable to the community.

We thank the reviewer for highlighting the potential value of this dataset to the community. It will be made publicly available on the NCBI website. We would like to clarify that our intention has always been to make this dataset publicly available; therefore, we take back any incorrect suggestions made in the original submission.

Reviewer #1 (Recommendations for the authors):

I would just recommend toning down the excitement about autoimmune TCRs being overrepresented in females. Then the conclusions will be in alignment with their results.

We thank the reviewer for this constructive recommendation. We would like to express our full support for the editorial transparency policies of eLife, which allow readers to access to both the reviewers’ comments and our detailed responses, enabling them to form their own informed opinions regarding our conclusions.

Nevertheless, we have moderated some of our wording.

Reviewer #2 (Public review):

Summary:

This study addresses the hypothesis that the strikingly higher prevalence of autoimmune diseases in women could be the result of biased thymic generation or selection of TCR repertoires. The biological question is important, and the hypothesis is valuable. Although the topic is conceptually interesting and the dataset is rich, the study has a number of major issues that require substantial improvement. In several instances, the authors conclude that there are no sex-associated differences for specific parameters, yet inspection of the data suggests visible trends that are not properly quantified. The authors should either apply more appropriate statistical approaches to test these trends or provide stronger evidence that the observed differences are not significant. In other analyses, the authors report the differences between sexes based on a pulled analysis of TCR sequences from all the donors, which could result in differences driven by one or two single donors (e.g., having particular HLA variants) rather than reflect sex-related differences.

Strengths:

The key strength of this work is the newly generated dataset of TCR repertoires from sorted thymocyte subsets (DP and SP populations). This approach enables the authors to distinguish between biases in TCR generation (DP) and thymic selection (SP). Bulk TCR sequencing allows deeper repertoire coverage than single-cell approaches, which is valuable here, although the absence of TRA-TRB pairing and HLA context limits the interpretability of antigen specificity analyses. Importantly, this dataset represents a valuable community resource and should be openly deposited rather than being "available upon request."

We thank the reviewer for highlighting the potential value of this dataset to the community. It will be made publicly available on the NCBI website. We would like to clarify that our intention has always been to make this dataset publicly available; therefore, we take back any incorrect suggestions made in the original submission.

Weaknesses:

Major:

The authors state that there is "no clear separation in PCA for both TRA and TRB across all subsets." However, Figure 2 shows a visible separation for DP thymocytes (especially TRA, and to a lesser degree TRB) and also for TRA of Tregs. This apparent structure should be acknowledged and discussed rather than dismissed.

We thank the reviewer for this careful observation. Discussing apparent “trends” rather than statistically significant results is indeed a nuanced issue, as over-interpretation of visual patterns is usually discouraged. We agree that, within the specific context of TCR repertoire analyses, visual structures in multivariate projections such as PCA can provide useful contextual information.

However, we have not identified a striking trend in our representation. We therefore chose to avoid overemphasizing these visual impressions in the text.

Supplementary Figures 2-5 involve many comparisons, yet no correction for multiple testing appears to be applied. After appropriate correction, all the reported differences would likely lose significance. These analyses must be re-evaluated with proper multiple-testing correction, and apparent differences should be tested for reproducibility in an external dataset (for example, the pediatric thymus and peripheral blood repertoires later used for motif validation).

As is standard in exploratory immunogenomic studies, including TCR repertoire analyses, our objective was to uncover broad biological patterns rather than to establish definitive statistical associations. In analyses that are discovery-oriented, correction for multiple testing, while essential in confirmatory contexts, is not mandatory and may even obscure meaningful trends by inflating type II error rates. Our objective was therefore to highlight consistent directional patterns across analytical layers, to guide future confirmatory work rather than to make categorical claims.

We also note that this comment somewhat contrasts with the earlier suggestion to discuss trends that are not statistically significant.

With regard to the proposal to verify our observations using an external dataset, we are in full agreement that independent confirmation would be beneficial. However, as reviewer 1 rightly emphasized, the generation of such datasets from sorted human thymocyte subsets is “heroic” and has rarely, if ever, been achieved. We are aware of no existing dataset that provides comparable material or analytical depth.

The available single-cell thymic dataset (Park et al., Science 2020) includes only a few hundred sequences per donor, which is significantly less than the number of sequences in our study. This limited dataset is not adequate for cross-validation or for representing the full complexity of thymic TCR repertoires.

As with the pediatric thymus dataset, the lack of statistical power in the dataset due to the small number of female subjects (only three) means that sex-related differences in V/J usage cannot be evaluated.

Finally, the peripheral blood dataset is not appropriate for validating thymic generation or selection processes, as it reflects post-thymic selection and antigen-driven remodeling, making it impossible to distinguish peripheral effects from thymic influences.

For these reasons, none of the currently available datasets provides a sufficiently clean or powerful framework to test the reproducibility of subtle sex-associated effects on thymic TCR repertoires. Nevertheless, we fully agree that confirmation in an independent and larger cohort will be an important next step to refine these exploratory findings and assess their generalizability to a broader human population.

Supplementary Figure 6 suggests that women consistently show higher Rényi entropies across all subsets. Although individual p-values are borderline, the consistent direction of change is notable. The authors should apply an integrated statistical test across subsets (for example, a mixed-effects model) to determine whether there is an overall significant trend toward higher diversity in females.

We agree that Rényi entropies tend to show a consistent direction of change across subsets, with slightly higher values observed in females. In this section, our objective was to provide a descriptive overview of diversity patterns for each thymic subset. This is because these subsets are biologically distinct and therefore require individual analysis, as we previously demonstrated using the same dataset (Isacchini et al, PRX Life. 2024). Therefore, while a mixed-effects approach could in principle be applied to test for an overall trend, such an analysis would rely on the assumption of a common sex effect across heterogeneous cell types.

It is important to note that the complete dataset has now been made publicly available, enabling interested researchers to perform additional integrative or model-based analyses to further explore these diversity trends.

Figures 4B and S8 clearly indicate enrichment of hydrophobic residues in female CDR3s for both TRA and TRB (excluding alanine, which is not strongly hydrophobic). Because CDR3 hydrophobicity has been linked to increased cross-reactivity and self-reactivity (see, e.g., Stadinski et al., Nat Immunol 2016), this observation is biologically meaningful and consistent with higher autoimmune susceptibility in females.

We thank the reviewer for this insightful comment.

As correctly noted, increased hydrophobicity at specific CDR3β positions has been linked to enhanced cross-reactivity and self-reactivity, as described by Stadinski et al. (Nat Immunol 2016), and we reference this work in the manuscript.

In our analysis corresponding to Figure 4B (TRB), hydrophobicity was quantified at the sequence level by computing, for each unique CDR3β sequence, the overall proportion of hydrophobic amino acids across the CDR3 loop. This approach aligns with that of Lagattuta et al. (Nat Immunol 2022), whose code we adapted to accommodate longer CDR3s. This global hydrophobicity metric captures overall composition, but, by its construction, does not account for positional context, the key mechanism implicated by Stadinski et al.

As outlined in our original Figure 4C, the results were obtained through a position-based amino acid analysis. For each CDR3β sequence, we extracted the amino acid at every IMGTdefined CDR3 position (p104–p118) and quantified, at each position, the percentage of unique sequences containing each amino acid. Positions p109 and p110 correspond to the p6–p7 sites highlighted by Stadinski et al. as functionally relevant for self-reactivity. This analysis evaluates positional composition independently of clonotype frequency, focusing specifically on hydrophobic amino acid classes.

Following the recommendation of the reviewer, the revised manuscript has removed alanine (which is only weakly hydrophobic) has been excluded from the hydrophobic residue set. With this refined definition, we observe a significant enrichment of hydrophobic amino acids at p109 in CD8 T cell repertoires from females, with similar but non-significant trends at p109 in DP and CD4 Teff cells and at p110 in CD8 cells (see new Figure 4C).

As outlined in the revised Methods, Results, and Discussion sections, Figure 4C focuses exclusively on positional hydrophobic amino acid usage. This was previously implicit, although it was noted in the legend and visually represented in the plots.

The majority of "hundreds of sex-specific motifs" are probably donor-specific motifs confounded by HLA restriction. This interpretation is supported by the failure to validate motifs in external datasets (pediatric thymus, peripheral blood). The authors should restrict analysis to public motifs (shared across multiple donors) and report the number of donors contributing to each motif.

We fully agree that donor-specific and HLA-restricted motifs represent a major potential confounder in repertoire-level comparisons. To minimize this potential bias, our analysis was explicitly restricted to public motifs, as clearly stated in the Materials and Methods section:

“Additional filters were applied so that: (i) a motif includes public CDR3aa sequences (shared by at least two individuals); (ii) a significant enrichment is detected (Fisher’s exact test, p < 0.01); and (iii) a usage difference between groups of at least twofold (Wilcoxon test, p < 0.05).”

Accordingly, every motif reported in the manuscript is supported by at least two independent donors, ensuring that no motif reflects an individual- or HLA-specific effect (see Supplementary Figures 10-13[previously Supplementary Figure 9]). We have now added a more explicit mention of the number of donors contributing to each motif in the figure legend and have clarified this point in the revised Methods and Results sections to make this criterion more visible to readers.

When comparing TCRs to VDJdb or other databases, it is critical to consider HLA restriction. Only database matches corresponding to epitopes that can be presented by the donor's HLA should be counted. The authors must either perform HLA typing or explicitly discuss this limitation and how it affects their conclusions.

We respectfully disagree with the assertion that HLA typing is necessary for the type of comparative analysis we have conducted. While it is true that HLA molecules present peptides to TCRs and thereby contribute to the tripartite interaction determining T cell activation, extensive evidence indicates that the CDR3 region, particularly CDR3β, is the dominant determinant of antigen specificity. This finding is supported by structural and computational studies (Madi et al., eLife, 2017; Huang et al., Nat. Biotech., 2020; MayerBlackwell et al., Methods Mol. Biol., 2022) showing that CDR3β residues are responsible for the majority of peptide contacts, whereas CDR1 and CDR2 primarily interact with the MHC framework.

As emphasized in several recent benchmarking studies (e.g., Springer et al., Front Immunol, 2021), CDR3β sequence composition alone captures most of the information required for specificity inference. Consequently, widely used and validated computational tools such as GIANA (Zhang et al. Nat. Commun. 2021), iSMART (Zhang et al. Clin. Cancer Res. 2020), and ATMTCR (Cai et al. Front. Immunol. 2022) rely exclusively on CDR3β aminoacid sequences and still achieve high predictive performance.

Our analysis aligns with this well-established paradigm. While we agree that integrating donor HLA typing would refine epitope-level annotation and reduce potential noise, the absence of HLA data does not invalidate the comparative framework we used, which focuses on relative representation of annotated specificities across groups rather than on individual TCR–HLA–peptide triads.

Although the age distributions of male and female donors are similar, the key question is whether HLA alleles are similarly distributed. If women in the cohort happen to carry autoimmuneassociated alleles more often, this alone could explain observed repertoire differences. HLA typing and HLA comparison between sexes are therefore essential.

To address the issue of any potential differences in HLA background, we examined the subset of adult donors for whom HLA typing information was available (HLA-A, HLA-B, HLADR, and HLA-DQB; n = 16). Within this subset, the distribution of HLA alleles was relatively balanced between males and females (as illustrated by the heatmap showing HLA class II expression patterns and HLA class I family grouping in Author response image 1). This analysis suggests that the sex-associated differences in the repertoire observed in our study are unlikely to be driven solely by unequal representation of autoimmune-associated HLA alleles.

We acknowledge, however, that complete HLA information was not available for all donors, which remains a limitation of the dataset.

Author response image 1.

In some analyses (e.g., Figures 8C-D) data are shown per donor, while others (e.g., Fig. 8A-B) pool all sequences. This inconsistency is concerning. The apparent enrichment of autoimmune or bacterial specificities in females could be driven by one or two donors with particular HLAs. All analyses should display donor-level values, not pooled data.

While Figures 8A–B present pooled data to summarize global trends, the corresponding donor-level analyses were provided in Supplementary Figures 15B and 16 (previously Supplementary Figures 11B and 12). In these, each individual is shown separately, with each point representing an individual. It is important to note that these donor-resolved plots do not reveal any sample-specific driver: the patterns observed in the pooled data remain consistent across donors, without any single individual accounting for the apparent enrichments. As outlined in the revised manuscript, readers now directed to the relevant supplementary figures for further clarification.

The reported enrichment of matches to certain specificities relative to the database composition is conceptually problematic. Because the reference database has an arbitrary distribution of epitopes, enrichment relative to it lacks biological meaning. HLA distribution in the studied patients and HLA restrictions of antigens in the database could be completely different, which could alone explain enrichment and depletions for particular specificities. Moreover, differences in Pgen distributions across epitopes can produce apparent enrichment artifacts. Exact matches typically correspond to high-Pgen "public" sequences; thus, the enrichment analysis may simply reflect variation in Pgen of specific TCRs (i.e., fraction of high-Pgen TCRs) across epitopes rather than true selection. Consequently, statements such as "We observed a significant enrichment of unique TRB CDR3aa sequences specific to self-antigens" should be removed.

We respectfully disagree with the conclusion that our enrichment analysis lacks biological meaning. Our approach directly involves a direct comparison of the same set of observed TCR sequences between males and females. Consequently, any potential biases related to generation probability (Pgen), which affect all sequences equally, cannot account for the observed sex-specific differences. To summarize, because the comparison is performed on the same set of sequences, changes in the probability of generation across epitopes cannot explain the differences seen between the sexes.

We do agree, however, that the composition of the reference databases may influence apparent enrichment patterns, as these resources contain uneven distributions of epitope categories and often incomplete information regarding HLA restriction. It should be noted that this limitation is inherent to all database-based annotation approaches, a fact which is explicitly acknowledged in the revised Discussion.

The overrepresentation of self-specific TCRs in females is the manuscript's most interesting finding, yet it is not described in detail. The authors should list the corresponding self-antigens, indicate which autoimmune diseases they relate to, and show per-donor distributions of these matches.

We thank the reviewer for this constructive suggestion.

As recommended, we have expanded the description of the self-specific TCRs identified in our dataset and now provide this information in Supplementary Table 2 of the revised manuscript. Specifically, the table lists the corresponding self-antigens and the autoimmune diseases with which they are associated. In our curated database, these annotations primarily correspond to celiac disease and type 1 diabetes, which were the two autoimmune contexts explicitly defined in the manually curated reference datasets.

For the “cancer” specificity group, we have clarified that antigen assignments were established based on (i) annotations available in the original databases (IEDB, VDJdb, McPAS-TCR) and (ii) cross-referencing with additional resources, including the Human Protein Atlas, the Cancer Antigenic Peptide Database (de Duve Institute), and the Cancer Antigen Atlas (Yi et al., iScience 2021), to ensure consistency in the classification of cancer and neoantigen specificities. Please refer to the Materials and Methods section for a full description of the procedure for this specific assignment.

Donor-level distributions of these self-specific matches are now shown in Supplementary Figures 15B and 16 (previously Supplemental Figures 11B and 12), allowing direct visualization of inter-donor variability. Importantly, these plots confirm that the observed enrichment in females is not driven by a single individual, further supporting the robustness of the finding.

The concept of poly-specificity is controversial. The authors should clearly explain how polyspecific TCRs were defined in this study and highlight that the experimental evidence supporting true polyspecificity is very limited (e.g., just a single TCR from Figure 5 from Quiniou et al.).

We certainly agree (and regret) that the concept of TCR polyspecificity remains a subject of debate and often underappreciated in the field of immunology. As Don Mason famously discussed in his seminal essay “A very high cross-reactivity is an essential feature of the TCR” (doi: 10.1016/S0167-5699(98)01299-7) published over 25 years ago, both theoretical and experimental evidence indicates that each TCR can, in principle, recognize millions of distinct peptides, albeit with variable avidity.

Although this principle is widely accepted, it is frequently overlooked in the field of experimental immunology. In this area, anything that deviates from strict monospecificity is often disregarded as noise.

In our own analyses of large-scale TCR repertoires, we have repeatedly observed that many CDR3 sequences are annotated with multiple specificities across different databases, often corresponding to peptides from unrelated organisms. As demonstrated in Quiniou et al. (eLife 2023), such polyreactive TCRs exhibit distinctive features, including biased physicochemical composition, and tend to be enriched in various biological contexts. In our preliminary study of such TCRs, which have the capacity to be specific for multiple viral- and self- epitopes, we hypothesized that they may serve as a first line of defense against pathogens and also be involved in triggering autoimmunity. We therefore consider it important to report this phenomenon rather than omit it, especially given its potential relevance to both protective immunity and autoimmunity.

In the present study, polyspecific TCRs were defined operationally as TRB CDR3aa sequences associated with a minimum of two distinct specificity groups, corresponding either to different microbial species or to multiple antigen categories within the curated database. Therefore, our definition captures broader antigenic groupings rather than epitope-level binding events.

We fully acknowledge that direct experimental evidence for true molecular-level polyspecificity remains limited. Indeed, as the reviewer notes, only a single TCR with multiepitope reactivity has been rigorously demonstrated to date (Quiniou et al.2023). Consequently, our analysis does not make claims about structural promiscuity; instead, it uses database-annotated cross-reactivity as a proxy to explore broader repertoire-level patterns.

As outlined in the Methods section, this definition has been clarified and its discussion expanded in the Discussion to explicitly address these conceptual and methodological nuances.

Minor:

Clarify why the Pgen model was used only for DP and CD8 subsets and not for others.

As noted, computing Pgen values involves two steps: (i) training a generative model of V(D)J recombination using IGoR, and (ii) estimating generation probabilities with OLGA based on that model. Both steps require a significant amount of computing power, especially when applied to large repertoires across multiple subsets. For this reason, we focused the analysis on DP thymocytes, which represent the repertoire prior to thymic selection, and CD8 T cells after CD8 selection.

The Methods section should define what a "high sequence reliability score" is and describe precisely how the "harmonized" database was constructed.

Briefly, the annotated database used in this study was constructed in accordance with the procedure established in our previously published work (Jouannet et al., NAR Genomics and Bioinformatics, 2025). The study integrates three publicly available resources, IEDB, VDJdb, and McPAS-TCR, which were collected as of October 2023. These three datasets were then merged into a single harmonized compendium, undergoing extensive standardization. When entries shared identical information across databases (same V–CDR3–J for both TRA and TRB, same epitope, organism, PubMed ID, and cell subset), only one representative was kept; discrepant or incomplete entries were retained to preserve information. We then assigned a sequence reliability score, the Verified Score (VS), following the verification strategy used by IEDB. The scale ranges from 0 to 2 and reflects the concordance between calculated and curated TRA/TRB CDR3 sequences (2 = both TRA and TRB present are verified, 1.1 = only TRA verified, 1.2 = only TRB verified, 0 = no verified chain). A second score, the Antigen Identification Score (AIS), is used to rank antigen-identification methods on a scale of 0 to 5, according to the strength of the experimental evidence supporting them.

In the present study, “high reliability” refers to sequences with a verified TRB CDR3aa chain (VS ≥ 1.2) and an AIS score corresponding to T cells in vitro stimulation with a pathogen, protein or peptide, or pMHC X-mer sorting (> 3.2, excluding categories 4.1 and 4.2), ensuring that downstream analyses were performed on a rigorously curated and biologically trustworthy dataset. The Methods section now explicitly details these criteria.

The statement "we generated 20,000 permuted mixed-sex groups" is unclear. It is not evident how this permutation corrects for individual variation or sex bias. A more appropriate approach would be to train the Pgen model separately for each individual's nonproductive sequences (if the number of sequences is large enough).

The objective of this analysis was to determine whether the enrichment of TRBV06-5 in females was due to random grouping of individuals or whether it was attributable to sex itself. To do so, we generated all possible perfectly mixed groups of donors (i.e., groups containing an equal number of male and female donors) for the concerned thymocyte subset, and then performed 20,000 random pairwise comparisons between such mixed groups. For each comparison, we tested the TRBV06-5 usage between the two mixed groups. This procedure directly evaluates whether group composition (independent of sex) could spuriously generate differences in TRBV usage. Notably, none of these 20,000 comparisons between the two mixed groups yielded a statistically significant difference in TRBV06-5 usage. In contrast, when comparing the true male and female groups, a significant difference was identified. This demonstrates that the signal we observe is not driven by random donor grouping or individual-level variation, but is specifically associated with sex. It is important to note that this analysis, which is designed to exclude spurious group effects, is rarely performed in published repertoire studies, yet it provides an important internal control for robustness.

Reviewer #2 (Recommendations for the authors):

(1) Data availability "upon request" is unacceptable. All raw and processed data, as well as scripts used for analysis and figure generation, must be publicly deposited before publication.

We would like to clarify that our intention has always been to make this dataset publicly available. It was a mistake to suggest otherwise in the original submission.

(2) At the beginning of the Results section, include a brief description of the dataset: number of donors, sex ratio, age range, number of samples per subset, and sorting strategy. Although Figure 1 shows this, the information should also be mentioned in the main text.

In line with the recommendation, we have now added a summary of the cohort characteristics at the beginning of the Results section. This includes the number of donors, sex ratio, age range, number of samples per subset, and the sorting strategy used. While this information was already included in Figure 1, we concur that including it directly in the main text enhances readability.

(3) Report the number of cells and unique clonotypes analyzed per individual. Rank-frequency plots (in log-log coordinates) would be helpful.

We have now added, for each donor and each subset, the number of cells, and additionally for each chain, the number of total and unique clonotypes analyzed. This information is provided in the revised manuscript in a new supplementary table (Supplemental Table 1).

These plots have been integrated into the revised manuscript as Supplementary Figure 2.

(4) For analysis in Figure 4B, the total fraction of hydrophobic amino acids should be calculated for each patient separately, and values for men and women should be compared (analogously to Figure 4C, but for the whole CDR3 and excluding alanine).

Please note that the TRB CDR3aa composition in Figure 4B has already been quantified at the individual level. For each unique TRB CDR3aa sequence, we computed the proportion of each of the 20 amino acids across the CDR3β loop, then summarized these values per donor (mean per individual). The log2 fold change displayed in Figure 4B (and supplemental Figure 9 for TRA) is calculated from the median donor-level values for females versus males, rather than from pooled CDR3s. It is intended as descriptive, “global” view of amino acid usage within the central CDR3 region. Hydrophobicity was not used directly in the computation, but is indicated only by bar color, based on the Kyte-Doolittle- derived IMGT classification. This provides an observational overview of amino acid composition in the central CDR3 region.

As the mechanistic link between hydrophobicity and self-reactivity described by Stadinski et al. is explicitly position-dependent, we consider positional analyses to be the most appropriate method for formally interrogating this hypothesis, as we did in Figure 4C. Here, our primary focus was on the position-specific usage of hydrophobic amino acids at IMGT positions p109-p110. These positions correspond to the central p6-p7 positions described by Stadinski et al. For each individual, we computed the proportion of unique TRB CDR3aa sequences carrying a hydrophobic amino acid at a given position.

Accordingly, in the revised manuscript we refined the Figure 4C by excluding alanine due to its weak hydrophobic property (as recommended by the reviewer) This positional composition analysis now reveals a statistically significant increase in hydrophobic usage at p109 in female CD8 repertoires, with similar, though non-significant, trends at p109 in DP and CD4Teff ad at p110 in CD8 cells. Figure 4B is therefore retained as an exploratory overview of amino acid composition usage along the CDR3 loop, while Figure 4C is used for the more specific question of hydrophobicity and potential cross-reactivity.

The Methods section has been expanded to provide clearer descriptions of these computations, and the Results and Discussion sections corresponding to Figures 4B-C (and supplemental Figure 9) have been revised to make the rationale, implementation, and interpretation of these hydrophobicity analyses more explicit.

(5) Figure 6 shows a trend toward higher clustering of Treg TCRs in males, which could relate to the lower incidence of autoimmunity in men. The authors could test whether specific Treg clusters are male-specific and shared among male donors.

As shown in Figure 6, a clear trend towards higher similarity among Treg CDR3aa sequences in males is evident, as indicated by the proportion of sequences included in clusters and in the overall similarity density. However, identifying “male-specific clusters” shared across donors is not straightforward in our analytical framework.

In our approach, for each cell subset, CDR3aa sequences were downsampled 100 times to the smallest sample size, and clustering was repeated at each iteration. Therefore, the clusters’ identities are not consistent across iterations. The clusters depend on the specific subset of sequences selected at each downsampling step, as well as on their underlying Pgen distribution. Therefore, it is not possible to reliably assess whether specific clusters are systematically “male-shared”. This is because cluster composition is a function of stochastic resampling rather than of biological structure. For this reason, a comparison of cluster identities across donors would not produce interpretable results.

Author response:

The following is the authors’ response to the original reviews

We thank the reviewers for their constructive feedback, which has helped preparing a substantially improved manuscript. In response to concerns about the conceptual distinction between prediction and stimulus dependency, we have fundamentally restructured the paper around the notion of passive control systems. This involved rewriting the Abstract, Introduction, and large portions of the Results (~60% of text revised).

Key changes:

- New analyses on Goldstein et al. (2022) data. We demonstrate that our findings—including the insufficiency of proposed corrections—generalise to the original dataset (Figures S2B, S3B, S5C, S6B).

- Clarified novel contribution. We now make explicit that prior control analyses (residualisation, bigram removal) do not address the concern, because hallmarks persist in passive systems that cannot predict.

- Proposed criterion for future work. Pre-onset neural encoding can only count as evidence for prediction if it exceeds a passive baseline (e.g., acoustics).

We believe the revision offers a clearer, more rigorous contribution and provides a constructive framework for evaluating claims of neural prediction.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This paper tackles an important question: What drives the predictability of pre-stimulus brain activity? The authors challenge the claim that "pre-onset" encoding effects in naturalistic language data have to reflect the brain predicting the upcoming word. They lay out an alternative explanation: because language has statistical structure and dependencies, the "pre-onset" effect might arise from these dependencies, instead of active prediction. The authors analyze two MEG datasets with naturalistic data.

Strengths:

The paper proposes a very reasonable alternative hypothesis for claims in prior work. Two independent datasets are analyzed. The analyses with the most and least predictive words are clever, and nicely complement the more naturalistic analyses.

Weaknesses:

I have to admit that I have a hard time understanding one conceptual aspect of the work, and a few technical aspects of the analyses are unclear to me. Conceptually, I am not clear on why stimulus dependencies need to be different from those of prediction. Yes, it is true that actively predicting an upcoming word is different from just letting the regression model pick up on stimulus dependencies, but given that humans are statistical learners, we also just pick up on stimulus dependencies, and is that different from prediction? Isn't that in some way, the definition of prediction (sensitivity to stimulus dependencies, and anticipating the most likely upcoming input(s))?

We thank the reviewer for this comment, which highlights that the previous version wasn’t sufficiently clear. Conceptually, the difference is critical: it is the difference between passively encoding or representing the stimulus (like e.g., a spectrogram of the stimulus would), and actively generating predictions.

We have substantially changed the framing of the paper to put the notion of control systems centre-stage. One such control system is the speech acoustics: they encode the stimulus (and thus its dependencies) but cannot predict. When we observe the "hallmarks of prediction" in acoustics, this demonstrates the hallmarks can arise without any prediction.

This brings me to some of the technical points: If the encoding regression model is learning one set of regression weights, how can those reflect stimulus dependencies (or am I misunderstanding which weights are learned)? Would it help to fit regression models on for instance, every second word or something (that should get rid of stimulus dependencies, but still allow to test whether the model predicts brain activity associated with words)? Or does that miss the point? I am a bit unclear as to what the actual "problem" with the encoding model analyses is, and how the stimulus dependency bias would be evident. It would be very helpful if the authors could spell out, more explicitly, the precise predictions of how the bias would be present in the encoding model.

Different weights are estimated per time point in the time-resolved regression. This allows the model to learn how the response to words unfolds, but also to learn different stimulus dependencies at each timepoint. Fitting on every second word would reduce but not eliminate the problem. Our control system approach provides a more principled test. We have clarified the mechanism in the Introduction (lines 82-90), explaining how correlations between neighbouring words allow the regression model to predict prior neural activity without assuming pre-activation.

Reviewer #2 (Public Review):

Summary:

At a high level, the reviewers demonstrate that there is an explanation for pre-word-onset predictivity in neural responses that does not invoke a theory of predictive coding or processing. The paper does this by demonstrating that this predictivity can be explained solely as a property of the local mutual information statistics of natural language. That is, the reason that pre-word onset predictivity exists could simply boil down to the common prevalence of redundant bigram or skip-gram information in natural language.

Strengths:

The paper addresses a problem of significance and uses methods from modern NeuroAI encoding model literature to do so. The arguments, both around stimulus dependencies and the problems of residualization, are compellingly motivated and point out major holes in the reasoning behind several influential papers in the field, most notably Goldstein et al. This result, together with other papers that have pointed out other serious problems in this body of work, should provoke a reconsideration of papers from encoding model literature that have promoted predictive coding. The paper also brings to the forefront issues in extremely common methods like residualization that are good to raise for those who might be tempted to use or interpret these methods incorrectly.

Weaknesses:

The authors don't completely settle the problem of whether pre-word onset predictivity is entirely explainable by stimulus dependencies, instead opting to show why naive attempts at resolving this problem (like residualization) don't work. The paper could certainly be better if the authors had managed to fully punch a hole in this.

We thank the reviewer for their assessment.

We believe our paper does punch the hole that can be punched, which is a hole in the method. Our control demonstrates that adjusting the features (X matrix) cannot address dependencies that persist in the signal itself (Y matrix). Because the hallmarks emerge in a system that cannot predict (even after linearly removing the previous stimulus) attributing pre-onset encoding performance to neural prediction (rather than stimulus structure) is fundamentally ambiguous, and different (e.g. variance partitioning) approaches would suffer from the same ambiguity. We have reframed the manuscript to make this argument more clearly.

Reviewer #3 (Public Review):

Summary:

The study by Schönmann et al. presents compelling analyses based on two MEG datasets, offering strong evidence that the pre-onset response observed in a highly influential study (Goldstein et al., 2022) can be attributed to stimulus dependencies, specifically, the auto-correlation in the stimuli—rather than to predictive processing in the brain. Given that both the pre-onset response and the encoding model are central to the landmark study, and that similar approaches have been adopted in several influential works, this manuscript is likely to be of high interest to the field. Overall, this study encourages more cautious interpretation of pre-onset responses in neural data, and the paper is well written and clearly structured.

Strengths:

(1) The authors provide clear and convincing evidence that inherent dependencies in word embeddings can lead to pre-activation of upcoming words, previously interpreted as neural predictive processing in many influential studies.

(2) They demonstrate that dependencies across representational domains (word embeddings and acoustic features) can explain the pre-onset response, and that these effects are not eliminated by regressing out neighboring word embeddings - an approach used in prior work.

(3) The study is based on two large MEG datasets, showing that results previously observed in ECoG data can be replicated in MEG. Moreover, the stimulus dependencies appear to be consistent across the two datasets.

We’d like to thank the reviewer for their comments on our preprint.

Weaknesses:

(1) To allow a more direct comparison with Goldstein et al., the authors could consider using their publicly available dataset.

We thank the reviewer for this suggestion. The Goldstein dataset was not publicly available when we conducted this research. However, we have now applied our control analyses to their stimulus material, and found that the exact same problem applies to their dataset, too.

We have added analyses of the Goldstein et al. (2022) podcast stimulus throughout the paper. Results are shown in Figures S2B, S3B, S5C, and S6B. Critically, we observe the same pattern: both hallmarks emerge in the acoustic control system, and residualisation fails to eliminate them. This demonstrates that our findings generalise to the very dataset used to establish pre-onset encoding as evidence for neural prediction.

(2) Goldstein et al. already addressed embedding dependencies and showed that their main results hold after regressing out the embedding dependencies. This may lessen the impact of the concerns about self-dependency raised here.

We thank the reviewer for raising this point, as it reveals we failed to convey a central argument in the previous version. Goldstein et al.'s control analysis did not address the concern. We show that even after the control analyses that Goldstein et al. perform (removing bigrams, regressing out embedding dependencies) the "hallmarks of prediction" still emerge when applying the analysis to a passive control system that by definition does not predict: the speech acoustics. We now also show this in their data.

To better convey this critical point, around the concept of "passive control systems". We now first establish that the hallmarks appear in acoustics (Figure 3), then show that residualisation fails to remove them (Figure 4). This makes explicit that any claim about "controlling for dependencies" must be validated against a system that cannot predict.

(3) While this study shows that stimulus dependency can account for pre-onset responses, it remains unclear whether this fully explains them, or whether predictive processing still plays a role. The more important question is whether pre-activation remains after accounting for these confounds.

We thank the reviewer for this question, and we agree that the question whether pre-activation occurs is an important and interesting one. However, we ask a different question in our study: Our goal is not to definitively establish whether the brain predicts during language processing; it is to scrutinise what counts as evidence for prediction, and to correct for some highly influential claims made in the literature. The reviewer asks whether pre-activation remains "after accounting for these confounds." But the point we are trying to make is that in this analytical framework, one cannot analytically account for these confounds: corrections to the X matrix leave dependencies in the data itself intact, as the acoustic control demonstrates.

We do offer recommendations for future work. The passive control systems approach can serve as a benchmark: pre-onset neural encoding (or decoding) can only count as evidence for prediction if it exceeds what is observed in a passive control system like acoustics (which is not what we observe). Additionally, the field could move toward less naturalistic stimuli with tighter experimental controls, reducing the correlations that make this attribution so difficult. Developing a new definitive test is beyond the scope of our paper, but we believe applying this benchmark is a necessary first step.

To make this clearer, we have rewritten the Discussion to explicitly state this criterion (lines 331-340) and to outline these recommendations for future work (lines 337-340). We have also added a paragraph extending our argument to decoding approaches (lines 343-354), noting that the same ambiguity applies regardless of analytical direction.

Recommendations for Authors:

Reviewer #1 (Recommendations for Authors):

As per my "Weakness" point, I would appreciate engagement with the conceptual point related to the difference between prediction and stimulus correlations. Most importantly, I hope the authors will spell out more explicitly which predictions their proposal makes, and how exactly those would be present in an encoding model.

Our proposal makes a clear prediction: if pre-onset encoding can be explained by stimulus dependencies (essentially a confound in the analysis) the same hallmarks should emerge in passive control systems that encode the stimulus but do not predict. We test this with word embeddings and speech acoustics, and both show hallmarks despite not doing any prediction.

Reviewer #2 (Recommendations for Authors):

I greatly enjoyed reading the paper and only have minor quibbles. The work is overdue and will no doubt be a valuable addition to the literature to push back on over-hyped claims about the implications of pre-word predictivity in neural response. I have few issues with the methods that the paper uses, they seem sensible and in line with previous work that has investigated these questions, and I did not find typos.

One point I would like to raise is whether or not there is a more effective solution to resolving the issues behind residualization that the paper demonstrates. The authors show that removing next-word information does not effectively resolve the problem that local relationships in the stimulus dataset pose. The challenge to me here seems to be that it is difficult to get a model to "not learn" a relationship that is learnable. I wonder if a better solution to this is to not try to get a model to exclude a set of information but instead to do some sort of variance partitioning where you train a model to predict the next-word representation from the current-word representation (as in the self-predictivity analysis) and then build an encoding model out of the predicted representation. Then, compare the pre-word-onset encoding performance of the prediction with the pre-word-onset encoding performance of the original representation. If the performance of the two models roughly matches, that would be strong evidence that most of what these models are capturing before word onset is just explainable by the stimulus dependencies, no?

We would like to thank the reviewer for their kind words and positive appraisal!

The proposed analysis is that if a linear proxy representation, w_hat_t – predicted linearly from w_{t-1} – yields pre-onset predictivity comparable to the actual w_t vector, this would support that the effect can be explained by stimulus dependencies. While this is an interesting alternative analysis, we would be cautious about the inverse conclusion: that if w_t outperforms the linear proxy w_hat_t, the residual variance must reflect true neural prediction.

This is because of our control system results. We show that even when we remove the "predictable" shared variance – which is similar to computing the difference between w_t and w_hat_t – the unique information still yields pre-onset predictivity, albeit reduced, in the passive acoustics that by definition cannot predict. Therefore, instead of developing an ever-more-clever way to "correct" for the problem by adjusting the X matrix, we focus on showing that the problem lies in the stimulus itself. For the revision, we focused on reframing the problem and hope we have punched a fuller hole in the logic by breaking down the fundamental issue more clearly and showing it applies to the stimulus material of Goldstein et al. (2022) as well.

Additionally, I would say that I was a bit confused about what was going on in the methods figures, to the point where I do not see the value in having them, but thankfully, the text was clear enough to resolve that confusion.

We are sad the methods illustration wasn’t helpful. In presentations we have found that the illustrations were generally helpful to bring the analysis across, e.g. the aspect of keeping the analysis identical but simply replacing the brain data with either word vectors (current Figure 2) and acoustics (current Figure 3). In the revision we have reorganised the schematics slightly, we introduce the acoustics as a control system earlier, to separately introduce residualisation and its insufficiency (Figure 4). We hope this helps

Reviewer #3 (Recommendations for Authors):

(1) My major concern is the extent to which this study offers new insights beyond what was already demonstrated in Goldstein's work. First, the embedding dependency highlighted by the authors seems somewhat expected, given how these embeddings are constructed: GloVe embeddings are based on word co-occurrence statistics, and GPT embeddings are combinations of embeddings of preceding words. More importantly, Goldstein et al. addressed this issue by regressing out neighboring word embeddings. This control was effective, as also confirmed by the current manuscript, and their main results remain. Therefore, the embedding dependency appears to have been properly accounted for in the earlier study.

Building on the previous point, I appreciate the analysis of dependencies across representational domains, which I see as the main novel contribution of this manuscript. I would encourage the authors to explore this aspect more deeply. If I understand correctly, stimulus dependencies may persist even after regressing out neighboring word embeddings due to two potential factors:

(a) Temporal dependencies in embeddings: since the regression of neighbor words is performed at the word level rather than over time, temporal dependency may remain.

(b) Cross-feature dependencies - specifically, correlations between embeddings and acoustic features.

Regarding the first factor, it is not entirely clear to me whether this is a real problem—i.e., whether word-level regression fails to remove temporal dependencies. A simulation could help clarify this and support the argument. While it's not essential, it would be valuable if the authors could propose a method to address this issue, or at least outline it as a direction for future work.

For the second point, it would be helpful for the authors to explicitly explain the potential relationship between word embeddings and acoustic features. Additionally, while correlations between features are a common problem in speech research, they are typically addressed by regressing out acoustic features early in the analysis (Gwilliams et al., 2022). It would strengthen the current findings if the authors could test whether the self-predictability persists even after controlling for neighboring embeddings and acoustic features.

We appreciate the extensive and detailed engagement with our work, which has been very useful in highlighting key unclarities and gaps we had to address.

We do believe our study goes well beyond what was shown by Goldstein, by identifying a fundamental limitation in their analysis, and showing that their purported control analyses do not in fact control for the problem. We’ll address the reviewers' sub-questions in turn.

(i) Why this offers crucial insights beyond Goldstein et al.

While Goldstein et al. indeed addressed embedding dependencies via residualization (or in their case projection), their conclusion relied on the assumption that any neural encoding surviving this "fix" must reflect genuine predictive pre-activation. Our study invalidates this assumption. By applying the residualization fix, we show that the "hallmarks of prediction" persist just as robustly in a passive control system that cannot predict (the speech acoustics) as in the neural data. (We also show this for bigram removal.)

This provides a key new insight: persistent pre-onset predictivity after “correction” is not evidence that the dependency issue was solved. Instead, because the same effect persists in a system that cannot predict (acoustics), the persistence of the hallmarks cannot be attributed to prediction. It demonstrates that the standard "fix" is mathematically insufficient to remove the confound, rendering the original evidence for neural prediction fundamentally ambiguous.

(ii) Why do dependencies/hallmarks persist after residualization?

Residualization successfully removes the linear dependency between the current embedding (w_t) and the previous embedding (w_{t-1}) within the feature space. However, it does not (and cannot) remove the dependency from language itself, and therefore from the brain which (in some format) encodes the linguistic stimulus. Language is massively redundant. Knowing the current word tells you something about what came before – acoustically, syntactically, semantically. As long as the embedding identifies the word, the regression model will re-learn this relationship. For instance, in the case of acoustics, even when using the corrected embedding, the regression will re-learn that certain words (e.g., "Holmes") tend to follow certain acoustic patterns (e.g., the acoustics of "Sherlock"). “This shows that correcting the embeddings is insufficient: the dependencies exist in language itself, and the model will re-learn them from any signal that encodes that language.”

(iii) Why not regress out the acoustics?

This is also why "regressing out acoustics" (as the reviewer suggests) would miss the point. We do not claim that acoustic features leak into the neural signal or that acoustics are a specific confound to be removed. Rather, we use acoustics as a “passive baseline”: a system that encodes the stimulus but cannot predict. That the method yields "hallmarks of prediction" in this baseline demonstrates these hallmarks are not valid evidence for prediction—regardless of what additional features one regresses out. This motivates our proposed criterion: future studies seeing evidence for neural pre-activation should not rest on finding pre-onset encoding per se, since passive systems show this too. Rather, it should require demonstrating that the brain signal contains more information about the upcoming word than the passive stimulus baseline.

As these aspects are fundamental to the interpretation of our study, we have fundamentally re-organised and re-wrote large parts of the paper. We hope it is much clearer now.

(2) To better compare to Goldstein's work, the author may consider performing the same analyses using their publicly available dataset.

This is a good suggestion. When we initially conducted this research, the Goldstein dataset was not yet publicly available. It now is, and we have applied our analyses to their stimulus material. The same problem emerges: the hallmarks of prediction appear in the acoustics of their podcast stimuli. Even after applying the control analyses, pre-onset predictivity is robust in their acoustics (indeed, in correlation terms, higher than reported for the neural data, so there is not more predictivity in the brain than in the stimulus material), confirming that the issue we identify applies to the original dataset. Results are shown in Figures S2B, S3B, S5C, and S6B.

(3) It is also interesting to show the predictability effect after word onsets for self-predictability analyses, for example, in Figure 2C. The predictability effect is not only reflected in pre-onset responses but also in post-onset responses, i.e., larger responses for unpredicted words. Whether the stimulus dependency mirror this effect?

Our paper focuses specifically on temporal dependencies – the capacity of the current word to predict the previous stimulus signal (e.g., previous acoustics, previous embeddings) – and how this mimics neural pre-activation. Post-onset analyses, by contrast, concerns the mapping between the current word and its concurrent signal, which involves fundamentally different mechanisms (e.g., mapping fidelity, frequency effects, acoustic clarity, word length) and would require the consideration of covariates of the attributes of the word post-onset to meaningfully interpret. Post-onset, there can be differences between predictable and non predictable words – e.g. sometimes unpredictable words are pronounced with more emphasis – which is why surprisal studies include a large range of covariates. However, this is not about stimulus dependencies or pre-activation, so we consider it is beyond scope of our study.

(4) The authors might consider reporting the encoding performance for the residual word embeddings, similar to Figure S6B in Goldstein's paper. This would allow us to determine whether pre-activation persists in the MEG responses and compare its pattern with the predictability of pre-onset acoustics.

We do report this analysis, in the revised supplement it is shown in Figure S7. We placed it in the supplement precisely because residualized embeddings are not the "fix" they appear to be: as we show, they still yield strong pre-onset predictivity in the passive acoustic baseline (Figure 4, S6), undermining their use as a control.

(5) The series of previous pre-activation analyses proposed fruitful findings, e.g., the difference between brain regions (Fig. S4, (Goldstein et al., 2022)) and the difference between listeners and speakers (Figure 2, (Zada et al., 2024)). Whether these observed differences can be explained by the stimulus dependency?

We appreciate this question. Our goal is to address the general logic of using pre-onset encoding as evidence for prediction, rather than to critique every finding in specific papers, especially as it pertains to a specific author. But briefly:

Speaker vs. Listener differences (Zada et al., 2024): Zada et al. report distinct temporal profiles: speaker encoding peaks pre-onset (planning?), whereas listener encoding peaks post-onset but shows a pre-onset "ramp." Our critique applies to interpreting this ramp as "prediction." However, this interpretation is not central to their paper, which focuses on speaker-listener coupling via shared embedding spaces. We leave the implications (which are clear enough) to the reader.

Regional differences (Goldstein et al., 2022): Encoding timecourses do vary across electrodes, as we also observe across MEG sources (and participants). But our point is logical: because pre-onset encoding does not necessarily reflect prediction, finding a channel with stronger pre-onset encoding does not mean that channel performs “more prediction”. For instance, one subject in the Armeni dataset showed higher pre-onset than post-onset encoding (and indeed activity) overall – but it would be implausible to conclude this subject "only predicts" and does not “process” or “listen”. More likely, this reflects differences in signal-to-noise, integration windows, or source contributions. The exact sources of these morphological differences are interesting but unclear, and speculating on them is beyond our scope.

(6) I appreciate that the authors have shared their code; however, some parts appear to be missing. For example, the script encoding_analysis.py only includes package-loading code.

Thank you for noticing, we have updated our code database.

(7) What do the error bars in the figures represent - for example, in Figure 1C? How many samples were included in the significance tests? The difference between the two curves appears small, yet it is reported as significant. Additionally, Figure S1 shows large differences between subjects and between the two MEG datasets. Do the authors have any explanation for these differences?

The shaded areas in our previous Figure 1c) show 95% confidence intervals computed over the 100 MEG sources identified to be part of the bilateral language system and the 10 cross-validation splits.

We do not have an elaborate explanation for the differences in encoding performance across the three subjects in the few-subject dataset. Instead, we interpret these differences as a likely consequence of substantial inter-individual variability in evoked responses, even at the source level, arising from differences in cortical folding and the orientation of underlying current dipoles. We deem this a likely explanation since different electrodes in Goldstein’s ECoG data also showed very different encoding profiles.

With respect to the multi-subject dataset, we suspect that the large differences stem most likely from two substantial differences: First, the acoustics were purposefully manipulated by the experimenters to reduce temporal dependence. This made it harder for listeners to concentrate on the stories and thereby might have potentially led to lower quality neural data. Furthermore, it reduced one form of stimulus dependency, namely the acoustic temporal dependencies, which could be exploited by the encoding model to reach higher encoding accuracies. Secondly, MEG has a notoriously poor signal-to-noise ratio, and the amount of data per participant (7.745 words as opposed to 85.719 in the few-subject dataset) might not have been enough to produce reliably high encoding results.

Finally, the current study is clear and convincing, and my suggestions are not intended to question its novelty or robustness. Rather, I believe the authors are in a strong position to address a critical question in language processing: whether pre-activation occurs. The authors have thoughtfully considered important confounds related to pre-onset responses. Adding some approaches to regressing out these confounds could be particularly helpful for determining whether a true pre-onset response remains.

We thank the reviewer again for their constructive feedback, suggestions and questions. To clarify, however, our goal is *not* to definitively attest to whether pre-activation occurs. Our goal is simply to scrutinise a specific method to test for linguistic prediction. This method purports to be an improvement on conventional post-onset (e.g. surprisal-based) methods, as it can directly investigate effects occurring prior to word onset. We have demonstrated fundamental limitations in the underlying logic of this method. We propose passive control systems as baselines against which claims of prediction should be evaluated. Against this baseline, the current evidence does not show unequivocal support for prediction: pre-onset encoding in the brain does not exceed that in the passive control. However, we do not conclude from this that pre-activation does not exist — that would require a different study entirely. Our aim is more methodological: to establish what should count as evidence for prediction, not to settle whether prediction occurs.

We would like to thank the reviewers and editors for their thoughtful feedback, which has been tremendously helpful in improving the paper.

Author response:

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

We sincerely thank the editor and both reviewers for their time and thoughtful feedback on our manuscript. We have carefully addressed all the concerns raised in the responses below and incorporated the suggested revisions into the manuscript.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors investigated the population structure of the invasive weed Lantana camara from 36 localities in India using 19,008 genome-wide SNPs obtained through ddRAD sequencing.

Strengths:

The manuscript is well-written, the analyses are sound, and the figures are of great quality.

Weaknesses:

The narrative almost completely ignores the fact that this plant is popular in horticultural trade and the different color morphs that form genetic populations are most likely the result of artificial selection by humans for certain colors for trade, and not the result of natural selfing. Although it may be possible that the genetic clustering of color morphs is maintained in the wild through selfing, there is no evidence in this study to support that. The high levels of homozygosity are more likely explained as a result of artificial selection in horticulture and relatively recent introductions in India. Therefore, the claim of the title that "the population structure.. is shaped by its mating system" is in part moot, because any population structure is in large part shaped by the mating system of the organism, but further misleading because it is much more likely artificial selection that caused the patterns observed.

The reviewer raises the possibility that the observed genetic patterns may have originated through the selection of different varieties by the horticultural industry. While it is plausible that artificial selection can lead to the formation of distinct morphs, the presence of a strong structure between them in the wild populations cannot be explained just based on selection. The observed patterns in the inbreeding coefficient and heterozygosity can indeed arise from multiple factors, including past bottlenecks, selection, inbreeding, and selfing. In the wild, different flower colour variants frequently occur in close physical proximity and should, in principle, allow for cross-fertilization. Over time, this gene flow would be expected to erode any genetic structure shaped solely by past selection. However, our results show no evidence of such a breakdown in structure. Despite co-occurring in immediate proximity, the flower colour variants maintain distinct genetic identities. This suggests the presence of a barrier to gene flow, likely maintained by the species' mating system. Moreover, the presence of many of these flower colour morphs in the native range—as documented through observations on platforms like iNaturalist—suggests that these variants may have a natural origin rather than being solely products of horticultural selection.

While it is plausible that horticultural breeding involved efforts to generate new varieties through crossing—resulting in the emergence of some of the observed morphs—even if this were the case, the dynamics of a self-fertilizing species would still lead to rapid genetic structuring. Following hybridization, just a few generations of selfing are sufficient to produce inbred lines, which can then maintain distinct genetic identities. As discussed in our manuscript, such inbred lines could be associated with specific flower colour morphs and persist through predominant self-fertilization. This mechanism provides a compelling explanation for the strong genetic structure observed among co-occurring flower colour variants in the wild.

To further validate this, we conducted a bagging experiment on Lantana camara inflorescences to exclude insect-mediated cross-pollination. The results showed no significant difference in seed set between bagged and open-pollinated flowers, supporting the conclusion that L. camara is primarily self-fertilizing in India. These results are included in the revised manuscript.

As the reviewer rightly points out, the mating system of a species plays a crucial role in shaping patterns of genetic structure. However, in many natural populations, structuring patterns are often influenced by a combination of factors such as selection, barriers to gene flow, and genetic drift. In some cases, the mating system exerts a more prominent influence at the microgeographic level, while in others, it can shape genetic structure at broader spatial scales. What is particularly interesting in our study is that - the mating system appears to shape genetic structure at a subcontinental scale. Despite the species having undergone other evolutionary forces—such as a genetic bottleneck and expansion due to its invasive nature—the mating system exerts a more pronounced effect on the observed genetic patterns, and the influence of the mating system is remarkably strong, resulting in a clear and consistent genetic structure across populations.

Reviewer #1 (Recommendations for the authors):

Lantana camara is a globally invasive plant as the authors mention in their manuscript, but this study only focuses on India. This should be reflected in the title.

The reviewer has suggested that the title should reflect the study area. Since our sampling covers nearly all regions in India, we believe the patterns observed here are likely representative of those in other parts of the invaded range. For this reason, we would prefer to retain the current heading.

It would be helpful if the pictures of the flowers in Figure 3 were larger to more clearly see the different colors.

As per the reviewers suggestion we have increased the size of the images to improve clarity.

Figure 4 could probably be moved to supplemental material, it does not add much to the results.

We feel it is important to reiterate that the patterns we observe in Lantana are consistent with what one would expect in any predominantly self-fertilizing species. It act as an additional proof and therefore, we believe it is important to retain this figure, as it effectively conveys this link.

Reviewer #2 (Public review):

Summary:

The authors performed a series of population genetic analyses in Lantana camara using 19,008 genome-wide SNPs data from 359 individuals in India. They found a clear population structure that did not show a geographical pattern, and that flower color was rather associated with population structure. Excess of homozygosity indicates a high selfing rate, which may lead to fixation of alleles in local populations and explain the presence of population structure without a clear geographic pattern. The authors also performed a forward simulation analysis, theoretically confirming that selfing promotes fixation of alleles (higher Fst) and reduction in genetic diversity (lower heterozygosity).

Strengths:

Biological invasion is a critical driver of biodiversity loss, and it is important to understand how invasive species adapt to novel environments despite limited genetic diversity (genetic paradox of biological invasion). Lantana camara is one of the hundred most invasive species in the world (IUCN 2000), and the authors collected 359 plants from a wide geographical range in India, where L. camara has invaded. The scale of the dataset and the importance of the target species are the strengths of the present study.

Weaknesses:

One of the most critical weaknesses of this study would be that the output modelling analysis is largely qualitative, which cannot be directly comparable to the empirical data. The main findings of the SLiM-based simulation were that selfing promotes the fixation of alleles and the reduction of genetic diversity. These are theoretically well-reported knowledge, and such findings themselves are not novel, although it may have become interesting these findings are quantitatively integrated with their empirical findings in the studied species. In that sense, a coalescent-based analysis such as an Approximate Bayesian Computation method (e.g. DIY-ABC) utilizing their SNPs data would be more interesting. For example, by ABC-based methods, authors can infer the split time between subpopulations identified in this study. If such split time is older than the recorded invasion date, the result supports the scenario that multiple introductions may have contributed to the population structure of this species. In the current form of the manuscript, multiple introductions were implicated but not formally tested.

Through our SLiM simulations, we aimed to demonstrate that a pattern of strong genetic structure within a location (similar to what we observed in Lantana camara) can arise under a predominantly self-fertilizing mating system. These simulations were not parameterized using species-specific data from Lantana but were intended as a conceptual demonstration of the plausibility of such patterns under selfing using SNP data. While the theoretical consequences of self-fertilisation have been widely discussed, relatively few studies have directly modelled these patterns using SNP data. Our SLiM simulations contribute to this gap and support the notion that the observed genetic structuring in Lantana may indeed result from predominant self-fertilisation. Therefore, we conducted these simulations ourselves for invasive plants to test whether the patterns we observed are consistent with expectations for a predominantly self-fertilising species.

Additionally, as suggested by the reviewer, we have performed demographic history simulations using fastsimcoal2 to investigate the divergence among different flower colour morphs. The results have been incorporated into the revised manuscript.

First, the authors removed SNPs that were not in Hardy-Weinberg equilibrium (HWE), but the studied populations would not satisfy the assumption of HWE, i.e., random mating, because of a high level of inbreeding. Thus, the first screening of the SNPs would be biased strongly, which may have led to spurious outputs in a series of downstream analyses.

Applying a HWE filter is a common practice in genomic data analysis because it helps remove potential sequencing or genotyping artefacts, which can otherwise bias downstream analyses. However, we understand that HWE filtering can also remove biologically informative loci and potentially bias the analysis, especially when a stringent cutoff is used. A strict filter might retain only loci that perfectly fit Hardy–Weinberg expectations and exclude sites influenced by real evolutionary processes like selection and/or inbreeding.

To balance this, we used a mild HWE filter, aiming to remove clear artefacts while retaining loci that may reflect genuine biological signals. Another reason for applying it is that many downstream tools, for example, admixture, assume the markers are neutral and not strongly deviating from HWE (although this assumption may not always hold). This helps in avoiding the complexity of the model.

Second, in the genetic simulation, it is not clear how a set of parameters such as mutation rate, recombination rate, and growth rate were determined and how they are appropriate.

We have cited the references for these values in the manuscript. However, for Lantana, many such baseline data are not available, so we used general values reported for plants, which is an accepted approach when working with understudied species. Moreover, the aim of these simulations was to develop a general understanding of how mating systems influence genetic diversity in invasive plants, rather than to parameterize the simulations specifically for Lantana.

While we acknowledge that this simulation does not provide an exact representation of the species' evolutionary history, the goal of the simulation was not to produce precise estimates but rather to illustrate the feasibility of such strong genetic structuring resulting from self-fertilisation alone.

Importantly, while authors assume the selfing rate in the simulation, selfing can also strongly influence the effective mutation rate (e.g. Nordborg & Donnelly 1997 Genetics, Nordborg 2000 Genetics). It is not clear how this effect is incorporated in the simulation.

In genetic simulations, it is often best to begin with simpler scenarios involving fewer parameters, and we followed this approach. As the reviewer rightly pointed out, selfing can influence multiple factors such as mutation and recombination rates. However, to first understand the broad effects, we chose to work with simpler scenarios where both mutation and recombination rates were kept constant.

Third, while the authors argue the association between flower color and population structure, their statistical associations were not formally tested.

We thank the reviewer for this valuable suggestion. We have performed a MANOVA to test the association between flower colour and genetic structure. These results are incorporated in the revised manuscript.

Also, it is not mentioned how flower color polymorphisms are defined. Could it be possible to distinguish many flower color morphs shown in Figure 1b objectively?

We carefully considered this and defined our criteria based on flower colour. Specifically, we named morphs according to the colour of both young and old flowers. If both stages shared the same colour, we used that colour as the name. As shown in Figure 1b, it is possible to reliably distinguish between the different flower colour morphs. While one could also measure flower colour using a photometer, we believe both approaches yield similar results.

I am concerned particularly because the authors also mentioned that flower color may change temporally and that a single inflorescence can have flowers of different colors (L160).

The flower colour changes within an inflorescence, with young flowers shifting colour after pollination. However, this trend is consistent within a plant; for example, the yellow–pink morph always changes from yellow to pink. Based on this consistency, we incorporated a naming system that considers both the colour of younger and older flowers.

Reviewer #2 (Recommendations for the authors):

Figure 4: Figures a and b are not the "signatures of high inbreeding", because such patterns could also simply happen due to geographical isolation. The title of the figure could be changed. Figure 4c should be presented as a histogram.

We have incorporated this suggestion into the manuscript and revised the figure title accordingly. However, we believe that presenting Figure 4c in its current form is more informative.

L459 "in the introduced range, Lantana is self-compatible": is it self-incompatible in the native range? If it is known, it could be mentioned in the manuscript.

A previous study from India demonstrated that self-fertilisation is possible in Lantana, providing an additional line of evidence for our findings. However, Lantana remains poorly studied in its native range, and to the best of our knowledge, only a single study has examined its pollination biology there, which we have cited in this paper.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this paper, Chen et al. identified a role for the circadian photoreceptor CRYPTOCHROME (cry) in promoting wakefulness under short photoperiods. This research is potentially important as hypersomnolence is often seen in patients suffering from SAD during winter times. The mechanisms underlying these sleep effects are poorly known.

Strengths:

The authors clearly demonstrated that mutations in cry lead to elevated sleep under 4:20 Light-Dark (LD) cycles. Furthermore, using RNAi, they identified GABAergic neurons as a primary site of cry action to promote wakefulness under short photoperiods. They then provide genetic and pharmacological evidence demonstrating that cry acts on GABAergic transmission to modulate sleep under such conditions.

Weaknesses:

The authors then went on to identify the neuronal location of this cry action on sleep. This is where this reviewer is much more circumspect about the data provided. The authors hypothesize that the l-LNvs which are known to be arousal-promoting may be involved in the phenotypes they are observing. To investigate this, they undertook several imaging and genetic experiments.

Major concerns:

(1) Figure 2 A-B: The authors show that knocking down cry expression in GABAergic neurons mimics the sleep increase seen in cryb mutants under short photoperiod. However, they do not provide any other sleep parameters such as sleep bout numbers, sleep bout duration, and more importantly waking activity measurements. This is an essential parameter that is needed to rule out paralysis and/or motor defects as the cause of increased "sleep". Any experiments looking at sleep need to include these parameters.

Thank you for bringing up these points. We have now included these sleep parameters in Figure 2—figure supplement 3.

(2) For all Figures displaying immunostaining and imaging data the resolution of the images is quite poor. This makes it difficult to assess whether the authors' conclusions are supported by the data or not.

We apologize for the poor resolution. This is probably due to the compression of the figures in the merged PDF file. We are now uploading the figures individually and hopefully this can resolve the resolution issue.

(3) In Figure 4-S1A it appears that the syt-GFP signal driven by Gad1-GAL4 is colabeling the l-LNvs. This would imply that the l-LNvs are GABAergic. The authors suggest that this experiment suggests that l-LNvs receive input from GABAergic neurons. I am not sure the data presented support this.

We agree that this piece of data alone is not sufficient to demonstrate that the l-LNvs receive GABAergic inputs rather than the l-LNvs are GABAergic. However, when nlsGFP signal is driven by two independent Gad1-GAL4 lines (one generated by P element insertion while the other generated by GAL4 inserted into the Gad1 locus), we do not observe any prominent signal in the l-LNvs (Figure 5A and B; Figure 5-figure supplement 1A). We have also co-labeled using Gad1GAL4 and PdfLexA (Figure 5-figure supplement 1B). As can be seen, Gad1GAL4-driven GFP signal is present only in the s-LNvs but not the l-LNvs. This further supports the idea that the l-LNvs are not GABAergic, and that the syt-GFP signal likely arises from GABAergic neurons projecting to the l-LNvs.

(4) In Figure 4-S1B. The GRASP experiment is not very convincing. The resolution of the image is quite poor. In addition, the authors used Pdf-LexA to express the post t-GRASP construct in l-LNvs, but Pdf-LexA also labels the s-LNvs, so it is possible that the GRASP signal the authors observe is coming from the s-LNvs and not the l-LNvs. The authors could use a l-LNvs specific tool to do this experiment and remove any doubts. Altogether this reviewer is not convinced that the data presented supports the conclusion "All in all, these results demonstrate that GABAergic neurons project to the l-LNvs and form synaptic connections." (Line 176). In addition, the authors could have downregulated the expression of Rdl specifically in l-LNvs to support their conclusions. The data they are providing supports a role for RDL but does not prove that RDL is involved in l-LNvs.

Thank you for these wonderful suggestions. Again we apologize for the poor resolution and hopefully by uploading the images separately we can resolve this issue. We agree that the GRASP signal could be coming from the s-LNvs and not the l-LNvs but unfortunately we are not able to find a LexA that is specifically expressed in the l-LNvs. We believe the trans-Tango data further support the idea that GABAergic neurons project to and form synaptic connections with the l-LNvs. Nonetheless, we have changed our conclusion to “All in all, these results strongly suggest that GABAergic neurons project to the l-LNvs and form synaptic connections” to be more rigorous. In addition, we have obtained R78G01GAL4 which is specifically expressed in the l-LNvs, and using this GAL4 to knock down Rdl rescues the long-sleep phenotype of cry mutants (Figure 4—figure supplement 1D).

(5) In Figures 4 A and C: it appears that GABA is expressed in the l-LNvs. Is this correct? Can the authors clarify this? Maybe the authors could do an experiment where they co-label using Gad1-GAL4 and Pdf-LexA to clearly demonstrate that l-LNvs are not GABAergic. Also, the choice of colors could be better. It is very difficult to see what GABA is and what is PDF.

Thank you for this wonderful suggestion. We have now co-labeled using Gad1GAL4 and PdfLexA (Figure 5-figure supplement 1B). As can be seen, Gad1GAL4-driven GFP signal is present only in the s-LNvs but not the l-LNvs. We suspect the GABA signal at the l-LNvs may arise from the GABAergic projections received by these cells. We have now changed the color of the GABA/PDF signals in these images and have reduced the intensity of the PDF signal. Hopefully, it would be easier to visualize in this revised version.

(6) Figure 4G: Pdf-GAL4 expresses in both s-LNvs and l-LNvs. So, in this experiment, the authors are silencing both groups, not only the l-LNvs. Why not use a l-LNvs specific tool?

Thank you for bring up this important point. We have previously used c929GAL4 to express Kir2.1 and this led to lethality. We have now used two l-LNv-specific GAL4 drivers (R78G01GAL4 and R10H10GAL4) that we newly obtained to express Kir2.1 but did not observe significant effect on sleep. Please see Author response image 1 for the results.

Author response image 1.

Daily sleep duration of male flies expressing Kir2.1 in l-LNvs using R78G01GAL4 (A)(n = 40, 41, 30 flies) and R10H10GAL4 (B) (n = 40, 41, 32 flies) and controls, monitored under 4L20D. One-way ANOVA with Bonferroni multiple comparison test was used to calculate the difference between experimental group and control group.

(7) Figure 4H-I: The C929-GAL4 driver expresses in many peptidergic neurons. This makes the interpretation of these data difficult. The effects could be due to peptidergic cells being different than the l-LNvs. Why not use a more specific l-LNvs specific tool? I am also confused as to why some experiments used Pdf-GAL4 and some others used C929-GAL4 in a view to specifically manipulate l-LNvs? This is confusing since both drivers are not specific to the l-LNvs.

Thank you for bring up these important points. We have now used the l-LNv-specific R10H10GAL4 and the results are more or less comparable with that of c929GAL4 (Figure 4I and K), i.e. activating the l-LNvs blocks the long-sleep phenotype of cry mutants. The reason PdfGAL4 is used in 4G is because c929GAL4 leads to lethality while the l-LNv-specific GAL4 lines do not alter sleep.

(8) Figure 5-S1B: Why does the pdf-GAL80 construct not block the sleep increase seen when reducing expression of cry in Gad1-GAL4 neurons? This suggests that there are GABAergic neurons that are not PDF expressing involved in the cry-mediated effect on sleep under short photoperiods.

Yes, this is indeed the conclusion we draw from this result, and we commented on this in the Discussion: “Moreover, inhibiting cry RNAi expression in PDF neurons does not eliminate the long-sleep phenotype of Gad1GAL4/UAScryRNAi flies. Therefore, we suspect that cry deficiency in other GABAergic neurons is also required for the long-sleep phenotype. Given that the s-LNvs are known to express CRY and appear to be GABAergic based on our findings here, we believe that CRY acts at least in part in the s-LNvs to promote wakefulness under short photoperiod.”

In conclusion, it is not clear that the authors demonstrated that they are looking at a cry-mediated effect on GABA in s-LNvs resulting in a modulation of the activity of the l-LNvs. Better images and more-suited genetic experiments could be used to address this.

Thank you very much for all the comments. They are indeed quite helpful for improving our manuscript. Hopefully, with images of higher quality and the additional experiments described above, we have now provided more evidence supporting our major conclusion.

Reviewer #2 (Public Review):

Summary:

The sleep patterns of animals are adaptable, with shorter sleep durations in the winter and longer sleep durations in the summer. Chen and colleagues conducted a study using Drosophila (fruit flies) and discovered that a circadian photoreceptor called cryptochrome (cry) plays a role in reducing sleep duration during day/night cycles resembling winter conditions. They also found that cry functions in specific GABAergic circadian pacemaker cells known as s-LNvs inhibit these neurons, thereby promoting wakefulness in the animals in the winter. They also identified l-LNvs, known as arousal-promoting cells, as the downstream neurons.

Strengths:

Detailed mapping of the neural circuits cry acts to mediate the shortened sleep in winter-like day/night cycles.

Weaknesses:

The supporting evidence for s-LNvs being GABAergic neurons is not particularly strong. Additionally, there is a lack of direct evidence regarding changes in neural activity for s-LNvs and l-LNvs under varying day/night cycles, as well as in cry mutant flies.

Thank you very much for all the comments. We have now expressed nlsGFP by two independent Gad1-GAL4 lines (one generated by P element insertion while the other generated by GAL4 inserted into the Gad1 locus), and positive signals in the s-LNvs can be observed (Figure 5A and B; Figure 5-figure supplement 1A). Hopefully, this can provide some further support regarding the s-LNvs being GABAergic neurons.

We have now examined GCaMP signals in the l- and s-LNvs of WT and cry mutants under 4L20D/12L12D. Please see Author response image 2 for the results. As can be seen, both WT and cry mutants show photoperiod-dependent changes. Interestingly, cry mutants show more prominent reduction of GCaMP signal in the l-LNvs compared to WT under 12L12D vs. 4L20D, but the sleep duration phenotype is observed only under 4L20D. Moreover, GCaMP signal is elevated in the s-LNvs of cry mutants relative to WT under 4L20D but decreased under 12L12D. These results indicate that there are distinct mechanisms regulating sleep under short vs. normal photoperiod (with CRY being dispensable under 12L12D), and the role of CRY in modulating the activity of these neurons are also photoperiod-dependent. Further in-depth characterizations are need to delineate these complex issues.

Author response image 2.<br /> Quantification of GCaMP6m signal intensity normalized to that of tdTomato under 12L12D and 4L20D (n = 25-45 cells). Student’s t-test: compared to WT, #P < 0.05, ##P < 0.01; 12L12D vs. 4L20D, *P < 0.05, ***P < 0.001.

Reviewer #3 (Public Review):

Summary:

In humans, short photoperiods are associated with hypersomnolence. The mechanisms underlying these effects are, however, unknown. Chen et al. use the fly Drosophila to determine the mechanisms regulating sleep under short photoperiods. They find that mutations in the circadian photoreceptor cryptochrome (cry) increase sleep specifically under short photoperiods (e.g. 4h light: 20 h dark). They go on to show that cry is required in GABAergic neurons. Further, they suggest that the relevant subset of GABAergic neurons are the well-studied small ventral lateral neurons that they suggest inhibit the arousal-promoting large ventral neurons via GABA signalling.

Strengths:

Genetic analysis to show that cryptochrome (but not other core clock genes) mediates the increase in sleep in short photoperiods, and circuit analysis to localise cry function to GABAergic neurons.

Weaknesses:

The authors' conclusion that the sLNvs are GABAergic is not well supported by the data. Better immunostaining experiments and perhaps more specific genetic driver lines would help with this point (details below).

(1) The sLNvs are well known as a key component of the circadian network. The finding that they are GABAergic would if true, be of great interest to the community. However, the data presented in support of this conclusion are not convincing. Much of the confocal images are of insufficient resolution to evaluate the paper's claims. The Anti-GABA immunostaining in Fig 4 and 5 seem to have a high background, and the GRASP experiments in Fig 4 supplement 1 low signal.

We apologize for the poor resolution. This is probably due to the compression of the figures in the merged PDF file. We are now uploading the figures individually and hopefully this can resolve the resolution issue. Unfortunately, the GABA immunostaining does not work very well in our hands and thus the background is high. We have now adjusted the images by changing the minimum lookup table (LUT) value in the green channel to 213, which removes all pixels below 213. This can remove background without changing the gray values, so the analysis is not affected. We have modified all images the exact same way and hopefully this can improve the contrast. Furthermore, we have now expressed nlsGFP by two independent Gad1-GAL4 lines (one generated by P element insertion while the other generated by GAL4 inserted into the Gad1 locus), and positive signals in the s-LNvs can be observed (Figure 5A and B; Figure 5-figure supplement 1A). Hopefully, this can provide some further support regarding the s-LNvs being GABAergic neurons.

Transcriptomic datasets are available for the components of the circadian network (e.g. PMID 33438579, and PMID 19966839). It would be of interest to determine if transcripts for GAD or other GABA synthesis/transport components were detected in sLNvs. Further, there are also more specific driver lines for GAD, and the lLNvs, sLNVs that could be used.

Thank you for these wonderful suggestions. Based on PMID 19966839, both the s-LNvs and l-LNvs express Gad1 and VGAT at a relatively low level, although here in our study Gad1GAL4 expression is observed only in the s-LNvs and not l-LNvs. We have commented on this in the 4th paragraph of Discussion: “One study using cell-type specific gene expression profiling demonstrates Gad1 and VGAT expression in both s-LNvs and l-LNvs, although with relatively low signal (Nagoshi et al., 2010). Here we observed that Gad1GAL4 is expressed in the s-LNvs, and their GABA intensity is reduced when we use R6GAL4 to knock down VGAT in these cells.” PMID 33438579 does not report expression of these genes in either s-LNvs or l-LNvs, likely due to insufficient sequencing depth. Furthermore, we have now used two l-LNv-specific GAL4 lines (R78G01GAL4 and R10H10GAL4) to conduct some of the experiments that we previously used c929GAL4 for, and obtained comparable results (Figure 4I and K).

(2) The authors' model posits that in short photoperiods, cry functions to suppress GABA secretion from sLNvs thereby disinhibiting the lNVs. In Fig 4I they find that activating the lLNvs (and other peptidergic cells) by c929>NaChBac in a cryb background reduces sleep compared to activating lLNVs in a wild-type background. It's not clear how this follows from the model. A similar trend is observable in Fig 4H with TRP-mediated activation of lNVs, although it is not clear from the figure if the difference b/w cryb vs wild-type background is significant.

Thank you for bring up this important point. This does appear to be counterintuitive. We suspect that in cry mutants, there is more inhibition occurring at the l-LNvs and thus the system may be particularly sensitive to their activation. Therefore, activating these neurons on the mutant background can result in a more prominent wake-promoting effect compared to that of WT.

Recommendations for the authors:

Our major concern centers around the claim that the sLNvs are GABAergic and secrete GABA onto the lLNVs. As it stands, this is not well supported by the data.

The authors could substantiate these findings by using more specific driver lines for GAD / vGAT (MiMic based lines are available that should better recapitulate endogenous expression). Transcriptomic data for circadian neurons are available, the FlyWire consortium also predicts neurotransmitter identities for specific neural circuits. These datasets could be mined for evidence to support the claim of sLNvs being GABAergic

Thank you for these wonderful suggestions. We have now used MiMic-based lines for Gad1 (BS52090, Mi{MIC}Gad1MI09277) and VGAT (BS23022, Mi{ET1}VGATMB01219) to knock down cry but unfortunately were not able to observe changes in sleep. Please see Author response image 3 for the results.

Author response image 3.

Daily sleep duration of male flies with cry knocked down in GABAergic neurons by Gad1GAL4 (A) (n = 30, 38, 50, 18, 31 flies) or VGATGAL4 (B) (n = 28, 38, 50, 18, 30 flies) monitored under 4L20D.One-way ANOVA with Bonferroni multiple comparison test: compared to UAS control, ###P < 0.001.

Furthermore, we have now included another Gad1GAL4 line which is generated by knocking GAL4 transgene into the Gad1 locus. We are also able to observe increased sleep when using this GAL4 to knock down cry, and positive signals in the s-LNvs can be observed when using this GAL4 to drive nlsGFP (Figure 2B; Figure 5-figure supplement 1A).

Based on PMID 19966839, both the s-LNvs and l-LNvs express Gad1 and VGAT at a relatively low level, although here in our study Gad1GAL4 expression is observed only in the s-LNvs and not l-LNvs. We have commented on this in the 4th paragraph of Discussion: “One study using cell-type specific gene expression profiling demonstrates Gad1 and VGAT expression in both s-LNvs and l-LNvs, although with relatively low signal (Nagoshi et al., 2010). Here we observed that Gad1GAL4 is expressed in the s-LNvs, and their GABA intensity is reduced when we use R6GAL4 to knock down VGAT in these cells.” The FlyWire does not have prediction for this particular circuit that we are interested in.

Further, many of the immunostaining images have high background / low signal - so better confocal images would help, as would the use of more specific driver lines for the lNVs as it is sometimes hard to distinguish the lLNvs from sLNvs.

We have now adjusted all images by changing the minimum lookup table (LUT) value in the green channel to 213 and that of the red channel to 279, which removes all pixels below 213 and 279, respectively. This can remove background without changing the gray values, so the analysis is not affected. We have modified all images the exact same way and hopefully this can improve the signal to noise ratio. We were not able to find a LexA line that is specifically expressed in the l-LNvs but we have found two l-LNv-specific GAL4 lines (R78G01GAL4 and R10H10GAL4). We used these lines to conduct some of the experiments that we previously used c929GAL4 for, and obtained comparable results (Figure 4I and 4K).

Additional specific comments are in the reviews above.

Minor points:

(1) Line 55: CRYPTOCHROME is misspelled.

This has been fixed.

(2) Line 140: The authors need to provide the appropriate references for the use of THIP and SKF-97541.

This has been added.

(3) Line 149: there are multiple GABA-A receptors in flies, the authors should acknowledge that. What about LccH3 or Grd?

Thank you for bring up this important point. Here we focused only on Rdl because it is the only GABA-A receptor known to be involved in sleep regulation. We have modified our description regarding this issue: “We tested for genetic interaction between cry and Resistant to dieldrin (Rdl), a gene that encodes GABA-A receptor in flies and has previously been shown to be involved in sleep regulation.”

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors developed a new autofocusing method, LUNA (Locking Under Nanoscale Accuracy), to address severe focus drift-a major challenge in time-lapse microscopy. Using this method, they tackle a fundamental question in bacterial cold shock response: whether cells halt growth and division following an abrupt temperature downshift. Overall, the experimental design, modeling, and data analysis are solid and well executed. However, several points require clarification or further support to fully substantiate the authors' conclusions.

Strengths:

(1) The LUNA method outperforms existing autofocusing systems with nanoscale precision over a large focusing range. The focusing time is reasonable for the presented experiments, and the authors note potential improvements by using faster motors and optimized control algorithms, suggesting broad applicability. The theoretical simulations and experimental validation provide solid support for the robustness of the method.

(2) Using LUNA, the authors address a long-standing question in bacterial physiology: whether cells arrest growth and division after an abrupt cold shock. Single-cell analyses monitoring the entire course of cold adaptation and steady-state growth reveal features that are obscured in bulk-culture studies: cells continue to grow at reduced rates with smaller cell sizes, resulting in an apparently unchanged population-level OD. The experiments are well designed and analyses are generally solid and largely support the authors' conclusions.

(3) The authors also propose a model describing how population-level OD measurements depend on cell dry mass density, volume, and concentration. This provides a valuable conceptual contribution to the interpretation of OD-based growth measurements, which remain a gold-standard method in microbiology.

We thank the reviewer for acknowledging the strengths of our study.

Weaknesses:

(1) It is unclear whether the author's model explaining the population-level OD during acclimation is broadly applicable. Most analyses focus on a shift from 37˚C to 14˚C, where the model agrees well with experimental data. However, in the 37˚C to 12˚C experiment, OD600 decreases after cold shock (Fig. 5e), and the computed OD does not match the experimental measurements (Fig. S16a). Although the authors attribute this discrepancy to a "complicated interplay," no further explanation is provided, which limits confidence in the model's general applicability.

Thank you for this careful evaluation regarding the model generality. In the experiment with a temperature shift from 37°C to 12°C, the measured OD600 values were 0.243 at 0 hours and 0.242 at 5 hours. In comparison, our model-computed OD600 values were 0.243 at 0 hours and 0.271 at 5 hours. The absolute difference between the measured and computed values at 5 hours is therefore 0.028.

Given the typical experimental variability in OD600 measurements and the limited linear range of the OD-to-biomass approximation (generally considered reliable below ~0.5), this deviation is quantitatively modest. We appreciate your valuable feedback and are happy to provide further clarification if needed.

(2) The manuscript proposes that cell-cycle progression becomes synchronized across the population after cold shock, but the supporting evidence is not fully convincing. If synchronization refers primarily to the uniform reduction in growth rate following cold shock, this could plausibly arise from global translation inhibition affecting all cells. However, the additional claim that "cells encountering a relatively late CSR will accelerate division to maintain synchronization" is not strongly supported by the presented data.

We appreciate your critical reading, which has helped us identify ambiguities in our terminology and strengthen the clarity of our work. Regarding the term “synchronization”, we would like to clarify that it refers to two different scenarios: (i) the synchrony in the timing of growth rate changes after cold shock. The cells initiate the slowdown in growth almost simultaneously, suggesting a highly coordinated, non-stochastic population-level response to cold shock; (ii) the synchrony in division cycle progression.

In the sentence you referenced “cells encountering a relatively late CSR will accelerate divisions to maintain synchronization”, we intended to describe that cells maintain consistent progression of the division cycle after cold shock, meaning that after the same number of elapsed cycles, different cells are at a similar stage in their division timing (Figure 4f, 4g, Figure S14). The term “accelerate” refers to our observation that cells which complete a given cycle later than others tend to have shorter subsequent inter-division intervals, thereby “catching up” to maintain alignment in cycle number across the population. We acknowledge that using “synchronization” in this scenario may be ambiguous, and we will replace it with more precise phrasing “progression of division cycle” to accurately convey this finding.

(3) Several technical terms used in the method development section are not clearly defined and may be unfamiliar to a broad readership, which makes it difficult to fully understand the methodology and evaluate its performance. Examples include depth of focus, focusing precision, focusing time, focusing frequency, and drift threshold value. In addition, the reported average focusing time per location (~0.6 s) lacks sufficient context, limiting the reader's ability to assess its significance relative to existing autofocusing methods.

Thank you for your valuable comments and suggestions. In response, we have added more detailed descriptions in the Methods section of the revised version.

The reviewer noted that the reported average focusing time (~0.6 s) lacks sufficient context, which may limit readers’ ability to assess its significance relative to existing autofocusing methods. We would like to clarify that the core innovation of this work lies in the proposed theoretical framework for autofocusing, which offers advantages over existing methods in terms of focusing precision and range. While focusing time is a practically relevant performance metric, it is primarily presented here as an implementation-dependent parameter rather than a central theoretical contribution of this study. In our experimental setup, an average focusing time of 0.6 s proved sufficient for routine timelapse imaging in microscopy, thereby demonstrating the practical usability of LUNA.

Reviewer #2 (Public review):

Summary:

This study presents LUNA, an autofocus method that compensates for focus drift during rapid temperature changes. Using this approach, the authors show that E. coli cells continue to grow and divide during cold shock, revealing a coordinated, multi-phase adaptation process that could not be deduced from traditional population measurements. They propose a scattering-theory-based model that reconciles the paradox between growth differences of the bacteria at the single-cell level vs population level.

Strengths:

(1) The LUNA approach is pretty creative, turning coma aberration from what is normally a nuisance into an exploit. LUNA enabled long-term single-cell imaging during rapid temperature downshifts.

(2) The authors show that the long-assumed growth arrest during cold shock from population-level measurements is misleading. At the single-cell level, bacteria do not stop growing or dividing but undergo a continuous, three-phase adaptation process. Importantly, this behavior is highly synchronized across the population and not based on bet-hedging.

(3) Finally, the authors propose a model to resolve a long-standing paradox between single-cell vs population behavior: if cells keep growing, why does optical density (OD) of the culture stop increasing? Using light-scattering theory, they show that OD depends not only on cell number but also on cell volume, which decreases after cold shock. As a result, OD can remain flat, or even decrease, despite continued biomass accumulation. This demonstrates that OD is not a reliable proxy for growth under non-steady conditions.

We thank the reviewer for acknowledging the strengths of our study.

Weaknesses:

(1) While the authors theoretically explain the advantages of LUNA over existing autofocus methods, it is unclear whether practical head-to-head comparisons have been performed, apart from the comparison to Nikon PFS shown in Video S1. As written, the manuscript gives the impression that only LUNA can solve this problem, but such a claim would require more systematic and rigorous benchmarking against alternative approaches.

Thank you for your insightful comment regarding the comparison of LUNA with other autofocus methods.

In our study, we primarily compared LUNA with the Nikon PFS system (as shown in Video S1) because Nikon PFS is one of the most widely used commercial autofocus systems in single-cell time-lapse imaging, and its manufacturer provides well-defined performance parameters (e.g., focusing precision within 1/3 depth-of-focus, response time <0.7 s), which facilitates a quantitative comparison. For other commercial systems, such as Olympus ZDC, Zeiss Definite Focus, Leica AFC, and ASI CRISP, the publicly available specifications are often less clearly defined, or are measured under inconsistent conditions, making a direct head-to-head comparison challenging and potentially misleading. Additionally, in our preliminary experiments, we also tested an Olympus microscope and observed severe focus drift during slow cooling processes. From a physical perspective, LUNA is specifically designed to meet the demanding requirements of single-cell experiments, including a wide focusing range and high precision, while existing commercial systems may not physically achieve the combination of range and accuracy needed for such extreme conditions.

(2) No mutants/inhibitors used to test and challenge the proposed model.

We agree that such approaches would provide valuable mechanistic insights and further strengthen the validation of the model presented in this study. In the current work, our primary goal was to introduce LUNA autofocusing method and demonstrate its capability to resolve bacterial cold shock response at the single-cell level with unprecedented precision. As such, we focused on characterizing the wild-type physiological dynamics under cold shock, which already revealed several previously unreported phenomena. We acknowledge that the use of genetic mutants or chemical inhibitors targeting specific cold shock proteins or regulatory pathways would be a logical and powerful next step to dissect the underlying molecular mechanisms and test the causality of the observed growth dynamics. We plan to address this in future work by incorporating such perturbations to further test and refine the model.

(3) Cells display a high degree of synchronization, but they are grown in confined microfluidic channels under highly uniform conditions. It is unclear to what extent this synchrony reflects intrinsic biology versus effects imposed by the microfluidic environment.

The reviewer raises a pertinent question regarding whether the observed high degree of cell synchronization represents an intrinsic biological phenomenon or an artifact induced by the microfluidic environment.

Over the past decade, microfluidic chips, including the specific design used in our work, have become a widely accepted and powerful tool in microbial physiology research. A broad consensus has emerged within the community that the microenvironment within these microchannels does not significantly interfere with or perturb the natural physiological behavior of microorganisms (Dusny, C. & Grünberger, Curr Opin Biotechnol. 63, 26-33 (2020)). This understanding is also supported by the fact that key findings obtained with microfluidic single-cell technologies are reproducible by other methods. For example, the adder model of cell-size homeostasis in E. coli firstly observed in microfluidic chips has been repeatedly validated by different methods (Taheri-Araghi, S. et al. Curr. Biol. 25, 385-391 (2015)). Therefore, while we acknowledge the importance of considering environmental effects, we are confident that the synchronization we report reflects the genuine biological dynamics of E. coli cells.

(4) To further test and generalize the model, it would be informative to also examine bacterial responses at intermediate temperatures rather than focusing primarily on a single cold-shock condition.

We thank the reviewer for this thoughtful suggestion. In designing our experiments, we aimed to study the bacterial cold shock response at the single-cell level. A key feature of this response is that it is typically triggered only when the temperature drops below a certain threshold within a short time duration. We therefore chose to lower the temperature from 37 °C to 14 °C as rapidly as possible. This approach allowed us to leverage the unique capabilities of LUNA while also providing an opportunity to explore this biological process in greater detail.

We agree that investigating bacterial responses across intermediate temperatures would be highly informative for understanding how temperature changes affect cellular physiology. However, this direction addresses a distinct scientific question that lies beyond the scope of the current work. We fully acknowledge its value and do have the intention to explore it in future studies.

Author response:

(1) Claim regarding NNDSVD initialization

Reviewer #1:

The authors state that "MPS is the first implementation of Constrained Non-negative Matrix Factorization (CNMF) with Nonnegative Double Singular Value Decomposition (NNDSVD) initialization." However, NNDSVD initialization is the default method in scikit-learn's NMF implementation and is also used in CaIMAN. I recommend rephrasing this claim in the abstract to more accurately reflect MPS's novelty, which appears to lie in the specific combination of constrained NMF with NNDSVD initialization, rather than being the first use of NNDSVD initialization itself.

We agree that our original phrasing was too broad. NNDSVD-family initialization is widely used in NMF implementations (e.g., scikit-learn) and is available within some pipeline components. We revised the abstract and main text to clarify our intended contribution: MPS seeds CNMF directly with NNDSVD-derived nonnegative factors as the primary initialization strategy, rather than relying on heuristic or greedy ROI-based seeding, integrated within a memory-efficient, end-to-end workflow for long-duration miniscope recordings.

(2) Installation issue on macOS

Reviewer #1:

At present, there are practical issues that limit the usability of the software. The link to the macOS installer on the documentation website is not functional. Furthermore, installation on a MacBook Pro was unsuccessful, producing the following error: "rsync(95755): error: ... Permission denied ...unexpected end of file."

We thank the reviewer for identifying the broken installer link and the macOS installation error. We fixed the macOS installer link on the documentation website and updated installation instructions to explicitly address common macOS permission-related failures (including rsync "Permission denied" errors that arise when attempting to write into protected directories without appropriate privileges). We re-tested installation on clean macOS systems and confirmed successful installation under the revised instructions.

(3) Validation, benchmarking, and cross-pipeline comparison

Reviewer #2:

A major limitation of this manuscript is that the authors don't validate the accuracy of their source extraction using ground-truth data or any benchmark against existing pipelines... Without this kind of validation, it is impossible to truly determine whether MPS produces biologically acceptable results... Considering one of the main benefits of MPS is its low memory demand and ability to run on unsophisticated hardware, the authors should include a figure that shows how processing times and memory usage scale with dataset sizes and differing pipelines... runtime comparisons on identical datasets processed through MPS, CaImAn, Minian, or CaliAli would be necessary to substantiate performance claims of MPS being "10-20X faster".

We thank the reviewers for their careful reading and for raising the question of biological validity, which we agree is central to any calcium imaging analysis tool. We would like to clarify, however, that MPS does not introduce a novel source extraction algorithm, and therefore the question of biological validity is not one that MPS alone can answer - nor should it be expected to. MPS is built on CNMF, the same mathematical framework underlying CaImAn and Minian. The contribution of MPS lies in its initialization strategy and parallelization architecture, which allow this proven framework to operate in the multi-hour recording regime.

To address the reviewers' request for a direct qualitative comparison, we will run MPS, CaImAn, Minian, and MIN1PIPE on a representative 10-minute real recording with clearly visible neurons. The figure will show the spatial components (ROI footprints) and representative temporal traces (ΔF/F) for all four pipelines on identical data. We anticipate that the spatial layouts and temporal dynamics will be highly concordant across pipelines, demonstrating that MPS produces biologically consistent output. We believe this side-by-side comparison will provide a clear demonstration that MPS output is comparable in quality to established tools on tractable recordings.

Regarding runtime comparison across pipelines, we will provide a table showing approximate processing times at three recording durations (5, 20, and 180 minutes). On short recordings, all pipelines are expected to complete successfully at different rates, whereas on long-duration recordings, this pipeline behavior is expected to diverge. We acknowledge that any single runtime benchmark reflects specific hardware and dataset characteristics and may not generalize to all configurations. We will therefore present these data as illustrative rather than definitive and will direct readers to the MPS documentation for guidance on hardware-specific tuning.

(4) Dataset description and scope of generalizability

Reviewer #2:

The current datasets used for validating MPS are not described in the manuscript. The manuscript appears to have 28 sessions of calcium imaging, but it is unclear if this is a single cohort or even animal, or whether these data are all from the same brain region. Importantly, the generalizability of parameter choices and performance could vary for others based on brain region differences, use of alternative calcium indicators...

We agree that the dataset description should be centralized and unambiguous. We added a dedicated Methods subsection stating that all results are based on a single, controlled experimental dataset consisting of 28 long-duration miniscope sessions acquired under consistent conditions (same brain region, calcium indicator, optical configuration, and acquisition parameters). This section explicitly specifies the number of animals, brain region, frame rate, field of view, session duration, and total data volume. We also clarified that conclusions are intended to evaluate MPS performance in this controlled long-duration setting rather than to claim universal parameter generalizability across brain regions, indicators, or optical systems.

(5) Parameter guidance and documentation

Reviewer #2:

...users should not be expected to blindly trust default or suggested parameter selections. Instead, users need guidance on what each modifiable parameter does to their data and how each step analysis output should be interpreted. Currently, the documentation and FAQ website linked to MPS installation does not do an adequate job of describing parameters or their optimization...

We agree that users should not blindly trust default or suggested parameters. We substantially expanded and centralized documentation by adding a parameter-selection walkthrough that explains what each modifiable parameter does, how it affects intermediate and final outputs, and how diagnostic plots generated at each stage should be interpreted. Rather than prescribing dataset-specific parameter values, we explicitly framed parameter selection as an iterative, hypothesis-driven process informed by experimental factors such as calcium indicator kinetics, lens size and numerical aperture, field of view, recording duration, and expected neuronal density. We consolidated previously dispersed explanations from the GitHub repository into a single documentation site and expanded figure descriptions to guide interpretation by less experienced users. A representative sample dataset and accompanying analysis code were made publicly available at https://github.com/ariasarch/MPS_Sample_Code to support parameter exploration on tractable data.

(6) Packaging and distribution

Reviewer #1:

...current best practices in software development increasingly rely on continuous integration and continuous deployment (CI/CD) pipelines to ensure reproducibility, testing, and long-term maintenance. In this context, it has become standard for Python packages to be distributed via PyPI or Conda. Without dismissing the value of standalone installers, the overall quality and sustainability of MPS would be greatly enhanced by also supporting conventional environment-based installations.

Regarding distribution more broadly: while our one-click installers are intended to reduce setup burden for non-programmers, we recognize the value of conventional environment-based distribution for longterm sustainability. We are exploring the feasibility of adding a standard PyPI and/or Conda installation pathway alongside the standalone installers. To ensure reproducibility across environments, all package dependencies are now explicitly version-pinned at installation time, eliminating environment drift as a source of irreproducibility.

We would note, however, that PyPI distribution alone does not fully resolve the reproducibility challenges inherent to scientific Python software. Even with version-pinned dependencies, downstream changes in the Python interpreter itself, compiled extension modules, and platform-specific build toolchains can silently alter numerical behavior in ways that are difficult to anticipate or control. Our standalone installers address this by shipping a complete, fixed execution environment, and we believe this remains a meaningful architectural advantage for ensuring long-term reproducibility - particularly for non-developer users who may not be in a position to diagnose subtle environment-related failures. We see PyPI/Conda support and standalone installers as complementary rather than equivalent approaches, and will pursue both where feasible.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Taken altogether, the experimental evidence favors an erosion-dominated process. However, a few minor questions remain regarding the models. Why does the equalfragmentation model predict no biomass transfer between size classes? To what extent, quantitatively, does the erosion model outperform the equal fragments model at capturing the biomass size distributions? Finally, why does the idealized erosion fail to capture the size distribution at late stages in Supplemental Figure S9 - would this discrepancy be resolved if the authors considered individual colony variances in cell adhesion (for instance, as hypothesized by the authors in lines 133-137)? I do not believe these questions curb the other results of the paper.

Our analysis in Figure 2 considers two size classes: small colonies (l < 5) and large colonies (l ≥ 5). The equal-fragment model predicts that the fracture of a large colony gives rise to two daughter fragments with half the biovolume. For an average colony of l = 25 in diameter, this corresponds to two daughter fragments with a diameter of l = 18, which is still in the large colony class. Sequential fragmentation events would be required to set a biomass transfer to the small size range (l < 5). However, the nearly exponential behavior of the fragmentation frequency function (Eq. 5) implies that subsequent fragmentation events are greatly slowed down. Therefore, the equal-fragments model predicts that the biomass transfer from large to small colonies during the first five hours of the experiment is negligible. This is in a sharp contrast with the erosion model, which transfers biomass to the small size class at every fragmentation event. The difference between the two fragmentation models is quantified in Figure 2D, with a negligible change in biomass size distribution for the equal-fragment model (horizontal dash-dotted line) and a strong increase of small colonies for the erosion model (curved dashed line). Hence, it is clear from Figure 2D that the erosion model outperforms the equal-fragment model by capturing the observed shift from large to small colonies. We have now described this more clearly in lines 231-233.

Nevertheless, the performance of the idealized erosion model is limited at late stages (Fig. S9D). We agree with the reviewer that this limitation could potentially be overcome with the introduction of variance in cell adhesion among colonies (as we hypothesized in lines 140142). However, this is not a trivial thing to do, as it would require additional free parameters and reduce the simplicity of the model. Therefore, we chose to restrain our model to the common assumptions of idealized fragmentation models widely used in literature (e.g. references 53-55).

Reviewer #2 (Public review):

Especially the introduction seems to imply that shear force is a very important parameter controlling colony formation. However, if one looks at the results this effect is overall rather modest, especially considering the shear forces that these bacterial colonies may experience in lakes. The main conclusion seems that not shear but bacterial adhesion is the most important factor in determining colony size. The writing could have done more justice to the fact that the importance of adhesion had been described elsewhere. This being said, the same method can be used to investigate systems where shear forces are biologically more relevant.

In this work we aimed to investigate the effects of shear forces over a wide range of values, extending beyond the regime of natural lakes into the strong mixing created by technological applications such as the bubble plumes that are applied in several lakes to suppress cyanobacterial blooms. The adhesion force between cells via, e.g., extracellular polysaccharides (EPS) play an essential role by controlling the resistance to shear-driven erosion, which has been quantified in our model by the fitting parameters S_i and q_i.

We agree with the reviewer that we have missed some literature on Microcystis colony formation via cell aggregation (i.e., cell adhesion), for which we apologize. In our new revision, we have now included several new references [30-34,36] and we now describe the findings of these earlier studies. Specifically, in the Introduction we now pay more attention to the role of cell adhesion by writing (lines 53-60):

“In contrast, cell aggregation (sometimes also called cell adhesion) can promote a rapid increase in colony size beyond the limit set by division rates, and may explain sudden rises in colony size in late bloom periods [26, 30, 31]. Aggregation rates depend on the stickiness of the colonies, which in turn is controlled by the EPS composition, pH, and ionic composition of water [27–29]. In particular, divalent cations such as Ca2+ can bridge negatively charged functional groups in EPS and therefore increase stickiness [32–34]. It has been shown that high levels of Ca2+ enhance cell aggregation in Microcystis cultures [35]. Moreover, cell aggregation can provide a fast defense against grazing [36]. Fluid flow plays an important role in cell aggregation by regulating the collision frequency between cells or colonies [6]. In addition, fluid flow ….”

Furthermore, in the Conclusions we added (lines 374-376):

“A previous study on colony aggregation at high Ca2+ levels observed similar morphological differences in colony formation [35]. There, an initial fast cell aggregation produced a sparse colony structure, followed by a more compact structure of the colonies associated with cell division”

Finally, we would like to clarify a difference in terminology between the reviewer’s comment and our work. The term cell adhesion is commonly used in microbiology to refer to adhesion of cells with a solid substrate. In our work, the adhesion mediated by EPS occurs between free-floating cells and colonies. To avoid any confusion, we chose to refer to this process as cell aggregation, in line with other literature on suspended particles.

Reviewer #2 (Recommendations for the authors):

The authors have expanded on the image analysis process but now report substantially different correction factors (λ2 =2.79 compared to 73.13 in the previous submission; λ3 =0.52 compared to 13.71 in the previous submission). Could the authors comment on how the analysis changed? These correction factors for N<5 appear particularly relevant for the aggregation experiments presented in Figure 3. For measurements involving only small colonies, as in Figure 3, are these correction factors still valid? In addition, does the timing of image acquisition, i.e. when the colonies are imaged, influence the correction factors applied in this study?

The description of the calibration process was improved in our earlier revision of the manuscript to improve clarity and remove unclear definitions. In the first version, the supplementary equation (S1) for the input variable N_p[i] was defined as the number of features per frame. This variable is dependent on the frame dimension (2048x2048 px for large colonies, l>5, and 400x400 px for small colonies). We believe that a more suitable input is the concentration distribution, which is normalized by frame area, and therefore invariant to frame dimensions and less prone to misinterpretations. For this reason, we adjusted this definition of N_p[i] in the revised version of the manuscript, so that it expresses the number of features per frame area (instead of per frame). These changes required the calibration constants, λ₂ and λ₃, to be updated in the manuscript by a factor of (400 px/2048 px)². This explains why these two calibration constants changed by a factor 0.038. This rescaling of the input variable N_p[i] and the calibration constants did not affect the final results of our calculations (Figures 2 and 3).

The authors use a moderate dissipation rate to stir the colonies, after which they allow them to sediment. How long were the particles allowed to sediment before measurements were taken? Intuitively, one might expect a greater number of colonies to be detected following sedimentation, yet the authors report only about one third of the colonies in the sedimented state. What accounts for this reduction? Furthermore, if higher shear rates are applied, do the results differ, for instance if particles are lifted further by the shear flow? Some more clarity would help other researchers to perform similar work.

The sedimentation of particles following an initial stir was applied only for creating a reference size distribution, displayed in the supplementary Figures S8-C and D. As one intuitively would expect, a higher concentration of colonies was detected after sedimentation (Fig. S8-C and D) than during the shear flow (Fig. S8-A and B). During all other experiments in our work, the applied dissipation rate was sufficient to ensure a uniform distribution of colonies in suspension throughout the parameter range, as described in lines 461-473.

In the caption of Figure S8 we have reported the number of colonies counted in small subsamples. These numbers are just small subsets of the total number of colonies contained in the entire volume of the cone-and-plate setup. A sub-sample with larger volume was measured during the shear flow in comparison to the sub-sample measured for the sedimented sample, leading to a larger number of counted colonies in panels A and B (N = 10776, combined) compared to panels C and D (N = 3066 and 1455, respectively).

However, when normalized for the volume of the sub-samples, the calculated concentration of colonies is higher for panels C and D (as shown in the graphs). We understand that the earlier caption description of Figure S8 was misleading, for which we apologize. In the revised version, we have adjusted the caption to better describe the quantity:

“Number of colonies counted during sampling …”

Line 797 contains an unfinished edit ("Figure ADD") that should be corrected.

The unfinished edit has been corrected in the newly revised manuscript. Thanks!

Author response:

The following is the authors’ response to the previous reviews

We appreciate the authors' efforts in addressing the concerns raised, particularly including a variance partitioning approach to analyse their data. Detailed feedback on the revised manuscript are below and we include a brief list of comments that we think the authors could address in the text: 

(1) Justify metric selection - Could you please include in the text and explanation for why only five behavioural metrics were highlighted out of the many you calculated?

We have added explanations throughout the manuscript clarifying the rationale for selecting these behavioral parameters, including in lines 467ff. and 531ff. In short, the five highlighted metrics were chosen because they capture key aspects of the behavioral repertoire and, importantly, can be consistently measured across all experimental conditions. Other parameters were excluded as they were only applicable under specific contexts and thus not suitable for cross-condition comparisons.

(2) Discuss ICC variation - We note that there is variation among the ICC scores for the different metrics you've studied. While this is expected, we ask that you acknowledge in the text that some traits show high repeatability and others low, and reflect this variation in the conclusions.

We have added an additional paragraph in the Discussion (lines 743ff.) addressing the variation in ICC values among behavioral traits. This new section highlights that some metrics show high repeatability while others exhibit lower consistency, and we discuss how this heterogeneity informs our conclusions about individual behavioral stability across contexts.

(3) Tone down general claims - Because of the above point, we recommend that you avoid overstating that individuality persists across all behaviours. Please clarify this in the Abstract and main text that it applies to some traits more than others.

We carefully reviewed the entire manuscript and revised the phrasing wherever necessary to avoid overgeneralization. Statements about individuality have been adjusted to clarify that consistent individuality can be measured in some behavioral traits more strongly than to others, both in the Abstract and throughout the main text.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors state the study's goal clearly: "The goal of our study was to understand to what extent animal individuality is influenced by situational changes in the environment, i.e., how much of an animal's individuality remains after one or more environmental features change." They use visually guided behavioral features to examine the extent of correlation over time and in a variety of contexts. They develop new behavioral instrumentation and software to measure behavior in Buridan's paradigm (and variations thereof), the Y-maze, and a flight simulator. Using these assays, they examine the correlations between conditions for a panel of locomotion parameters. They propose that inter-assay correlations will determine the persistence of locomotion individuality.

Strengths: 

The OED defines individuality as "the sum of the attributes which distinguish a person or thing from others of the same kind," a definition mirrored by other dictionaries and the scientific literature on the topic. The concept of behavioral individuality can be characterized as: (1) a large set of behavioral attributes, (2) with inter-individual variability, that are (3) stable over time. A previous study examined walking parameters in Buridan's paradigm, finding that several parameters were variable between individuals, and that these showed stability over separate days and up to 4 weeks (DOI: 10.1126/science.aaw718). The present study replicates some of those findings, and extends the experiments from temporal stability to examining correlation of locomotion features betweendifferent contexts. 

The major strength of the study is using a range of different behavioral assays to examine the correlations of several different behavior parameters. It shows clearly that the inter-individual variability of some parameters is at least partially preserved between some contexts, and not preserved between others. The development of highthroughput behavior assays and sharing the information on how to make the assays is a commendable contribution.

Weaknesses:

The definition of individuality considers a comprehensive or large set of attributes, but the authors consider only a handful. In Supplemental Fig. S8, the authors show a large correlation matrix of many behavioral parameters, but these are illegible and are only mentioned briefly in Results. Why were five or so parameters selected from the full set? How were these selected? Do the correlation trends hold true across all parameters? For assays in which only a subset of parameters can be directly compared, were all of these included in the analysis, or only a subset?

The correlation analysis is used to establish stability between assays. For temporal retesting, "stability" is certainly the appropriate word, but between contexts it implies that there could be 'instability'. Rather, instead of the 'instability' of a single brain process, a different behavior in a different context could arise from engaging largely (or entirely?) distinct context-dependent internal processes, and have nothing to do with process stability per se. For inter-context similarities, perhaps a better word would be "consistency".

The parameters are considered one-by-one, not in aggregate. This focuses on the stability/consistency of the variability of a single parameter at a time, rather than holistic individuality. It would appear that an appropriate measure of individuality stability (or individuality consistency) that accounts for the high-dimensional nature of individuality would somehow summarize correlations across all parameters. Why was a multivariate approach (e.g. multiple regression/correlation) not used? Treating the data with a multivariate or averaged approach would allow the authors to directly address 'individuality stability', along with the analyses of single-parameter variability stability.

The correlation coefficients are sometimes quite low, though highly significant, and are deemed to indicate stability. For example, in Figure 4C top left, the % of time walked at 23°C and 32°C are correlated by 0.263, which corresponds to an R2 of 0.069 i.e. just 7% of the 32°C variance is predictable by the 23°C variance. Is it fair to say that 7% determination indicates parameter stability? Another example: "Vector strength was the most correlated attention parameter... correlations ranged... to -0.197," which implies that 96% (1 - R2) of Y-maze variance is not predicted by Buridan variance. At what level does an r value not represent stability?

The authors describe a dissociation between inter-group differences and interindividual variation stability, i.e. sometimes large mean differences between contexts, but significant correlation between individual test and retest data. Given that correlation is sensitive to slope, this might be expected to underestimate the variability stability (or consistency). Is there a way to adjust for the group differences before examining correlation? For example, would it be possible to transform the values to ingroup ranks prior to correlation analysis?

What is gained by classifying the five parameters into exploration, attention, and anxiety? To what extent have these classifications been validated, both in general, and with regard to these specific parameters? Is increased walking speed at higher temperature necessarily due to increased 'explorative' nature, or could it be attributed to increased metabolism, dehydration stress, or a heat-pain response? To what extent are these categories subjective?

The legends are quite brief and do not link to descriptions of specific experiments. For example, Figure 4a depicts a graphical overview of the procedure, but I could not find a detailed description of this experiment's protocol.

Using the current single-correlation analysis approach, the aims would benefit from rewording to appropriately address single-parameter variability stability/consistency (as distinct from holistic individuality). Alternatively, the analysis could be adjusted to address the multivariate nature of individuality, so that the claims and the analysis are in concordance with each other.

The study presents a bounty of new technology to study visually guided behaviors. The Github link to the software was not available. To verify successful transfer or openhardware and open-software, a report would demonstrate transfer by collaboration with one or more other laboratories, which the present manuscript does not appear to do. Nevertheless, making the technology available to readers is commendable.

The study discusses a number of interesting, stimulating ideas about inter-individual variability, and presents intriguing data that speaks to those ideas, albeit with the issues outlined above.

While the current work does not present any mechanistic analysis of inter-individual variability, the implementation of high-throughput assays sets up the field to more systematically investigate fly visual behaviors, their variability, and their underlying mechanisms. 

Comments on revisions:

While the incorporation of a hierarchical mixed model (HMM) appears to represent an improvement over their prior single-parameter correlation approach, it's not clear to me that this is a multivariate analysis. They write that "For each trait, we fitted a hierarchical linear mixed-effects model in Matlab (using the fit lme function) with environmental context as a fixed effect and fly identity (ID) as a random intercept... We computed the intraclass correlation coefficient (ICC) from each model as the betweenfly variance divided by total variance. ICC, therefore, quantified repeatability across environmental contexts."

Does this indicate that HMM was used in a univariate approach? Can an analysis of only five metrics of several dozen total metrics be characterized as 'holistic'?

Within Figure 10a, some of the metrics show high ICC scores, but others do not. This suggests that the authors are overstating the overall persistence and/or consistency of behavioral individuality. It is clear from Figure S8 that a large number of metrics were calculated for each fly, but it remains unclear, at least to me, why the five metrics in Figure 10a are justified for selection. One is left wondering how rare or common is the 0.6 repeatability of % time walked among all the other behavioral metrics. It appears that a holistic analysis of this large data set remains impossible. 

We thank the reviewer for the careful and thoughtful assessment of our work.

We have added an additional paragraph in the Discussion (lines 743ff.) explicitly addressing the variation in ICC values among behavioral traits. This section emphasizes that while some metrics show high repeatability, others exhibit lower consistency, and we discuss how this heterogeneity informs our conclusions regarding individual behavioral stability across contexts.

Regarding the reviewer’s concern about the analytical approach, we would like to clarify that the hierarchical linear mixed model (LMM) was applied in a univariate framework—each behavioral metric was analyzed separately to estimate its individual ICC value. This approach allows us to quantify repeatability for each trait across environmental contexts while accounting for individual identity as a random effect. Although this is not a multivariate model in the strict sense, it represents an improvement over the prior pairwise correlation approach because it explicitly partitions within- and between-individual variance.

As for the selection of behavioral metrics, the five parameters highlighted (% time walked, walking speed, vector strength, angular velocity, and centrophobicity) were chosen because they represent key, biologically interpretable dimensions of locomotor and spatial behavior and, importantly, could be measured reliably across all tested conditions. Several other parameters that we routinely analyze (e.g., Linneweber et al., 2020) could not be calculated in all contexts—for instance, under darkness or when visual cues were absent—and therefore were excluded to maintain consistency across assays.

We agree that a truly holistic multivariate comparison across all extracted parameters would be valuable; however, given the contextual limitations of some metrics, such an analysis was not feasible in the present framework. We have clarified these points in the revised manuscript to avoid potential misunderstandings.

The authors write: "...fly individuality persists across different contexts, and individual differences shape behavior across variable environments, thereby making the underlying developmental and functional mechanisms amenable to genetic dissection." However, presumably the various behavioral features (and their variability) are governed by different brain regions, so some metrics (high ICC) would be amenable to the genetic dissection of individuality/variability, while others (low ICC) would not. It would be useful to know which are which, to define which behavioral domains express individuality, and could be targets for genetic analysis, and which do not. At the very least, the Abstract might like to acknowledge that inter-context consistency is not a major property of all or most behavioral metrics.

We thank the reviewer for this helpful comment and agree that not all behavioral traits exhibit the same degree of inter-context consistency. We have clarified this point in the revised Abstract and ensured that it is also reflected in the main text. The Abstract now reads: 

“We find that individuality is highly context-dependent, but even under the most extreme environmental alterations tested, consistency of behavioral individuality always persisted in at least one of the traits. Furthermore, our quantification reveals a hierarchical order of environmental features influencing individuality. We confirmed this hierarchy using a generalized linear model and a hierarchical linear mixed model. In summary, our work demonstrates that, similar to humans, fly individuality persists across different contexts (albeit worse than across time), and individual differences shape behavior across variable environments. The presence of consistency across situations in flies makes the underlying developmental and functional mechanisms amenable to genetic dissection.” 

This revision clarifies that individuality is not uniformly expressed across all behavioral metrics, but rather in a subset of traits with higher repeatability, which are the most promising targets for future genetic analyses.

I hold that inter-trial repeatability should rightly be called "stability" while inter-context repeatability should be called "consistency". In the current manuscript, "consistency" is used throughout the manuscript, except for the new edits, which use "stability". If the authors are going to use both terms, it would be preferable if they could explain precisely how they define and use these terms.

We thank the reviewer for drawing attention to this inconsistency in terminology. We apologize for the oversight and have corrected it throughout the manuscript to ensure uniform usage.

Reviewer #2 (Public review):

Summary:

The authors repeated measured the behavior of individual flies across several environmental situations in custom-made behavioral phenotyping rigs.

Strengths:

The study uses several different behavioral phenotyping devices to quantify individual behavior in a number of different situations and over time. It seems to be a very impressive amount of data. The authors also make all their behavioral phenotyping rig design and tracking software available, which I think is great and I'm sure other folks will be interested in using and adapting to their own needs.

Weaknesses/Limitations: 

I think an important limitation is that while the authors measured the flies under different environmental scenarios (i.e. with different lighting, temperature) they didn't really alter the "context" of the environment. At least within behavioral ecology, context would refer to the potential functionality of the expressed behaviors so for example, an anti-predator context, or a mating context, or foraging. Here, the authors seem to really just be measuring aspects of locomotion under benign (relatively low risk perception) contexts. This is not a flaw of the study, but rather a limitation to how strongly the authors can really say that this demonstrates that individuality is generalized across many different contexts. It's quite possible that rank-order of locomotor (or other) behaviors may shift when the flies are in a mating or risky context. 

I think the authors are missing an opportunity to use much more robust statistical methods. It appears as though the authors used pearson correlations across time/situations to estimate individual variation; however far more sophisticated and elegant methods exist. The problem is that pearson correlation coefficients can be anticonservative and additionally, the authors have thus had to perform many many tests to correlate behaviors across the different trials/scenarios. I don't see any evidence that the authors are controlling for multiple testing which I think would also help. Alternatively, though, the paper would be a lot stronger, and my guess is, much more streamlined if the authors employ hierarchical mixed models to analyse these data, which are the standard analytical tools in the study of individual behavioral variation. In this way, the authors could partition the behavioral variance into its among- and withinindividual components and quantify repeatability of different behaviors across trials/scenarios simultaneously. This would remove the need to estimate 3 different correlations for day 1 & day 2, day 1 & 3, day 2 & 3 (or stripe 0 & stripe 1, etc) and instead just report a single repeatability for e.g. the time spent walking among the different strip patterns (eg. figure 3). Additionally, the authors could then use multivariate models where the response variables are all the behaviors combined and the authors could estimate the among-individual covariance in these behaviors. I see that the authors state they include generalized linear mixed models in their updated MS, but I struggled a bit to understand exactly how these models were fit? What exactly was the response? what exactly were the predictors (I just don't understand what Line404 means "a GLM was trained using the environmental parameters as predictors (0 when the parameter was not change, 1 if it was) and the resulting individual rank differences as the response"). So were different models run for each scenario? for different behaviors? Across scenarios? what exactly? I just harp on this because I'm actually really interested in these data and think that updating these methods can really help clarify the results and make the main messages much clearer!

I appreciate that the authors now included their sample sizes in the main body of text (as opposed to the supplement) but I think that it would still help if the authors included a brief overview of their design at the start of the methods. It is still unclear to me how many rigs each individual fly was run through? Were the same individuals measured in multiple different rigs/scenarios? Or just one?

I really think a variance partitioning modeling framework could certainly improve their statistical inference and likely highlight some other cool patterns as these methods could better estimate stability and covariance in individual intercepts (and potentially slopes) across time and situation. I also genuinely think that this will improve the impact and reach of this paper as they'll be using methods that are standard in the study of individual behavioral variation

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors): 

I am delighted to see the authors have included hierarchical models in their analysis. I really think this strengthens the paper and their conclusions while simultaneously making it more accessible to folks that typically use these types of methods to investigate these patterns of individual behavior. It's also cool, and completely jives with my own experience measuring individual behavior in that the activity metrics show the highest repeatability compared to the more flexible behaviors (such as "exploration"). I think it's quite striking and interesting to see such moderate repeatability estimates in these behaviors across what could be very different environmental scenarios. I think this is a very strong and meaty paper with a lot of information to digest producinghowever a very elegant and convincing take-home message: individuals are unique in their behavior even across very different environments.

We sincerely thank the reviewer for the positive and encouraging feedback, as well as for their valuable input throughout the review process. We are very pleased that the inclusion of hierarchical models and the resulting interpretations resonated with the reviewer’s own experience and perspective.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Our goal was to propose a possible computational mechanism underlying information integration in the claustrum, not to claim structural or causal equivalence between the model and the biological circuit. We acknowledge that some expressions in the original manuscript may have been interpreted as exceeding this intention, and we will revise the text to explicitly soften such statements.

It is well established that behavior-trained RNNs can admit multiple internal solutions capable of producing the same behavioral output, and we fully agree with this point. Among the many possible solutions, we focused on networks that exhibited dynamical properties consistent with independently obtained behavioral and physiological findings. Thus, in our view, biological plausibility in this study is not grounded in structural isomorphism, but rather in whether the core population-level dynamical properties observed in the model are reproducible in actual claustral population activity.

We also agree with the reviewer that our original qualitative comparison of GPFA-based latent trajectories did not provide sufficient quantitative support. In the revised manuscript, we have therefore added an eigenvalue-based quantitative analysis of the dimensional structure of population trajectories. This analysis does not depend on the identity of the dimensionality-reduction method itself, but instead focuses on quantifying the geometric structure of population-state trajectories as they evolve over time. Applying the same metric to both the RNN and biological claustrum data revealed consistent condition-specific differences in population dynamics.

This quantitative addition strengthens the previous qualitative trajectory comparison and clarifies that the model implements a specific computational dynamical regime that directionally corresponds to claustral population activity. While this does not imply uniqueness of the model, we believe it suggests that the proposed computational principle represents a biologically realizable candidate mechanism.

(1) Tone of model-data correspondence

Numerous statements describe the RNN as "closely mimicking," "recapitulating," or being "nearly identical" to claustral neural dynamics, sometimes extending to claims about causal relationships between neural activity and behavior. Given that neural data were not used to train the model, and that only a small subset of trained networks showed the reported dynamics, these statements should be substantially softened throughout the manuscript. The RNN should be framed as providing one possible computational realization consistent with existing data, not as a close instantiation of the biological circuit.

We agree with the reviewer’s concern. Expressions such as “closely mimicked,” “nearly identical,” and “recapitulate” will be replaced with more moderate language.

(2) Non-uniqueness of RNN solutions

The fact that only a small fraction of trained networks exhibited "claustrum-like" clusters deserves deeper discussion. This observation raises the possibility that the identified solution is fragile or highly specific rather than canonical. The authors should explicitly discuss the non-uniqueness of internal solutions in behavior-trained RNNs, including the range of alternative network dynamics that can reproduce the same behavior. In particular, it should be clarified why the specific network exhibiting "claustrum-like" clusters is informative about claustral computation, rather than representing one arbitrary solution among many.

As the reviewer noted, behavior-trained RNNs can yield multiple internal solutions that generate the same behavioral output, and we acknowledge this non-uniqueness. However, we do not interpret the relatively low success rate (5/100 networks) as evidence of fragility. Rather, we interpret it as suggesting that the emergence of this particular dynamical regime requires stringent structural constraints.

The computational demands of the task—specifically, the integration of temporally separated signals—drive convergence toward networks capable of sustaining persistent activity through recurrent excitatory connectivity. Indeed, all networks exhibiting a claustrum-like cluster shared a strong recurrent excitatory structure within Cluster 1, a structural feature consistent with our slice electrophysiology findings.