Author response:

The following is the authors’ response to the original reviews

eLife Assessment

This manuscript makes valuable contributions to our understanding of cell polarisation dynamics and its underlying mechanisms. Through the development of a computational pipeline, the authors provide solid evidence that compensatory actions, whether regulatory or spatial, are essential for the robustness of the polarisation pattern. However, a more comprehensive validation against experimental data and a proper estimation of model parameters are required for further characterization and predictions in natural systems, such as the C. elegans embryo.

We sincerely thank the editor(s) for their pertinent assessment. We have carefully considered the constructive recommendations and made the necessary revisions in the manuscript, which are also detailed in this response letter. We have implemented most of the revisions requested by the reviewers. For the few requests we did not fully accept, we have provided justifications. The corresponding revisions in both the Manuscript and Supplementary Information are highlighted with a yellow background. To provide a more comprehensive validation against experimental data and model parameters used for characterizing and predicting natural systems, we reproduced the qualitative and semi-quantitative phenomenon in three more experimental groups previously published (Section 2.5; Fig. S8) [Gotta et al., Curr. Biol., 2001; Aceto et al., Dev. Biol., 2006]. Combined with the original experiments (Section 2.5; Fig. S7) [Hoege et al., Curr. Biol., 2010; Beatty et al., Development, 2010; Beatty et al., Development, 2013], now we have reproduced five experimental groups in total (two acting on LGL-1 and three on CDC-42), comprising eight perturbed conditions and using wild-type as the reference. These results effectively demonstrate how comprehensively the network structure and parameters capture the characteristics of the C. elegans embryo. We have also acknowledged the limitations of the current cell polarization model and provided, in 2. Results and 3. Discussion and conclusion, a detailed outline of potential model improvements.

Joint Public Review:

The polarisation phenomenon describes how proteins within a signalling network segregate into different spatial domains. This phenomenon holds fundamental importance in biology, contributing to various cellular processes such as cell migration, cell division, and symmetry breaking in embryonic morphogenesis. In this manuscript, the authors assess the robustness of stable asymmetric patterns using both a previously proposed minimal model of a 2-node network and a more realistic 5-node network based on the C. elegans cell polarisation network, which exhibits anterior-posterior asymmetry. They introduce a computational pipeline for numerically exploring the dynamics of a given reaction-diffusion network and evaluate the stability of a polarisation pattern. Typically, the establishment of polarisation requires the mutual inhibition of two groups of proteins, forming a 2-node antagonistic network. Through a reaction-diffusion formulation, the authors initially demonstrate that the widely-used 2-node antagonistic network for creating polarised patterns fails to maintain the polarised pattern in the face of simple modifications. However, the collapsed polarisation can be restored by combining two or more opposing regulations. The position of the interface can be adjusted with spatially varied kinetic parameters. Furthermore, the authors show that the 5-node network utilised by C. elegans is the most stable for maintaining polarisation against parameter changes, identifying key parameters that impact the position of the interface.

We sincerely thank the editor(s) for the pertinent summary!

While the results offer novel and insightful perspectives on the network's robustness for cell polarisation, the manuscript lacks comprehensive validation against experimental data, justified node-node network interactions, and proper estimation of model parameters (based on quantitative measurements or molecular intensity distributions). These limitations significantly restrict the utility of the model in making meaningful predictions or advancing our understanding of cell polarisation and pattern formation in natural systems, such as the C. elegans embryo.

We sincerely thank the editor(s) for the comment!

To provide a more comprehensive validation against experimental data and model parameters, we reproduced the qualitative and semi-quantitative phenomenon in three more experimental groups previously published (Section 2.5; Fig. S8) [Gotta et al., Curr. Biol., 2001; Aceto et al., Dev. Biol., 2006]. Combined with the original experiments (Section 2.5; Fig. S7) [Hoege et al., Curr. Biol., 2010; Beatty et al., Development, 2010; Beatty et al., Development, 2013], now we have reproduced five experimental groups in total (two acting on LGL-1 and three on CDC-42), comprising eight perturbed conditions and using wild-type as the reference. These meaningful predictions effectively demonstrate the utility of our model’s network structure and parameters in advancing our understanding of cell polarisation and pattern formation in natural systems, exemplified by the C. elegans embryo.

We have also acknowledged the limitations of the current cell polarization model and provided, in 2. Results and 3. Discussion and conclusion, a detailed outline of potential model improvements. The limitations include, but are not limited to, issues involving “node-node network interactions” and the “proper estimation of model parameters (based on quantitative measurements or molecular intensity distributions)”, both of which rely on experimental measurements of biological information.   However, comprehensive experimental measurement data on every molecular species, their interactions, and each species’ intensity distribution in space and time were not fully available from prior research. Refinement is lacking for some of these interactions, potentially requiring years of additional experimentation. Moreover, for certain species at specific developmental stages, only relative (rather than absolute) intensity measurements are available. We agreed that such information is essential for establishing a more utilizable model and discussed it thoroughly in 3. Discussion and conclusion. From a theoretical perspective, we adopted assumptions from the previous literature and constructed a minimal model for a specific cell polarization phase to investigate the network's robustness, supported by five experimental groups and eight perturbed conditions in the C. elegans embryo.

The study extends its significance by examining how cells maintain pattern stability amid spatial parameter variations, which are common in natural systems due to extracellular and intracellular fluctuations. The authors found that in the 2-node network, varying individual parameters spatially disrupt the pattern, but stability is restored with compensatory variations. Additionally, the polarisation interface stabilises around the step transition between parameter values, making its localisation tunable. This suggests a potential biological mechanism where localisation might be regulated through signalling perception.

We sincerely thank the editor(s) for the pertinent review!

Focusing on the C. elegans cell polarisation network, the authors propose a 5-node network based on an exhaustive literature review, summarised in a supplementary table. Using their computational pipeline, they identify several parameter sets capable of achieving stable polarisation and claim that their model replicates experimental behaviour, even when simulating mutants. They also found that among 34 possible network structures, the wild-type network with mutual inhibition is the only one that proves viable in the computational pipeline. Compared with previous studies, which typically considered only 2- or 3-node networks, this analysis provides a more complete and realistic picture of the signalling network behind polarisation in the C. elegans embryo. In particular, the model for C. elegans cell polarisation paves the way for further in silico experiments to investigate the role of the network structure over the polarisation dynamics. The authors suggest that the natural 5-node network of C. elegans is optimised for maintaining cell polarisation, demonstrating the elegance of evolution in finding the optimal network structure to achieve certain functions.

We sincerely thank the editor(s) for the pertinent review!

Noteworthy limitations are also found in this work. To simplify the model for numerical exploration, the authors assume several reactions have equivalent dynamics, reducing the parameter space to three independent dimensions. While the authors briefly acknowledge this limitation in the "Discussion and Conclusion" section, further analysis might be required to understand the implications. For instance, it is not clear how the results depend on the particular choice of parameters. The authors showed that adding additional regulation might disrupt the polarised pattern, with the conclusion apparently depending on the strength of the regulation. Even for the 5-node wild-type network, which is the most robust, adding a strong enough self-activation of [A], as done in the 2-node network, will probably cause the polarised pattern to collapse as well.

We sincerely thank the editor(s) for the comment!

Now we have thoroughly expanded our acknowledgment of the model’s limitations in in 2. Results and 3. Discussion and conclusion. To rule out the equivalent dynamics assumption undermines our conclusions, we have added simulations showing that the cell polarization pattern stability does not depend on the exact strength of each regulation, provided the regulations on both sides are initially balanced as a whole (Fig. S5). Specifically, we used a Monte Carlo method to sample a wide range of various parameter values ( i.e., γ, α, k₁, k₂, q₁, q₂ and [X_c) for all nodes and regulations in simple 2-node network and C. elegans 5-node network, to achieve pattern stability. Under these conditions (i.e., without any reduction in the parameter space), single-sided self-regulation, single-sided additional regulation, and unequal system parameters still cause the stable polarized pattern to collapse, consistent with our conclusions in the simplified conditions with the parameter space reduced to three independent dimensions.

Additionally, the authors utilise parameter values that are unrealistic, fail to provide units for some of them, and assume unknown parameter values without justification. The model appears to have non-dimensionalised length but not time, resulting in a mix of dimensional and non-dimensional variables that can be confusing. Furthermore, they assume equal values for Hill coefficients and many parameters associated with activation and inhibition pathways, while setting inhibition intensity parameters to 1. These arbitrary choices raise concerns about the fidelity of the proposed model in representing the real system, as their selected values could potentially differ by many orders of magnitude from the actual parameters.

We sincerely thank the editor(s) for the comment!

We apologize for the confusion. The non-dimensionalised parameter values are adopted from previous theoretical research [Seirin-Lee et al., Cells, 2020], which originates from the experimental measurement in [Goehring et al., J. Cell Biol., 2011; Goehring et al., Science, 2011]. With the in silico time set as 2 sec per step, now we have added the Supplemental Text justifying how the units are removed during non-dimensionalization. This demonstrates that the derived non-dimensionalized parameter in this paper achieves realistic values on the same order of magnitude as those observed in reality, confirming the fidelity of the proposed model in representing the real system.

The assumption of “equal values for Hill coefficients and many parameters associated with activation and inhibition pathways” is to reduce the parameter space for affordable computational cost. It is a widely-used strategy to fix Hill coefficients [Seirin-Lee et al., J. Theor. Biol., 2015; Seirin-Lee, Bull. Math. Biol., 2021] and unify parameter values for different pathways in network research about both cell polarization [Marée et al., Bull. Math. Biol., 2006; Goehring et al., Science, 2011; Trong et al., New J. Phys., 2014] and other biological topics (e.g., plasmid transferring in the microbial community [Wang et al., Nat. Commun., 2020]), to control computational cost. Nevertheless, to rule out that the equivalent dynamics assumption undermines our conclusions, we have added simulations showing that the cell polarization pattern stability does not depend on the exact parameter values associated with activation and inhibition pathways, provided the regulations on both sides are initially balanced as a whole (Fig. S5). Specifically, we used a Monte Carlo method to sample a wide range of various parameter values (i.e_., _γ, α, k₁, k₂, q₁, q₂ and [X_c) for all nodes and regulations in simple 2-node network and C. elegans 5-node network, to achieve pattern stability. Under these conditions ( i.e., without any reduction in the parameter space), single-sided self-regulation, single-sided additional regulation, and unequal system parameters still cause the stable polarized pattern to collapse, consistent with our conclusions in the simplified conditions with the parameter space reduced to three independent dimensions.

To confirm the fidelity of the proposed model in representing the real system, we reproduced the qualitative and semi-quantitative phenomenon in three more experimental groups previously published (Section 2.5; Fig. S8) [Gotta et al., Curr. Biol., 2001; Aceto et al., Dev. Biol., 2006]. Combined with the original experiments (Section 2.5; Fig. 5; Fig. S7) [Hoege et al., Curr. Biol., 2010; Beatty et al., Development, 2010; Beatty et al., Development, 2013], now we have reproduced five experimental groups in total (two acting on LGL-1 and three on CDC-42), comprising eight perturbed conditions and using wild-type as the reference. These results effectively demonstrate how comprehensively the network structure and parameters capture the characteristics of the C. elegans embryo. We have also acknowledged the limitations of the current cell polarization model and provided, in 2. Results and 3. Discussion and conclusion, a detailed outline of potential model improvements.

It is worth noting that, although a strict match between numerical and realistic parameter values with consistent units is always helpful, a lot of notable pure numerical studies successfully unveil principles that help interpret [Ma et al., Cell, 2009] and synthesize real biological systems [Chau et al., Cell, 2012]. These studies suggest that numerical analysis in biological systems remains powerful, even when comprehensive experimental data from prior research are not fully available.

The definition of stability and its evaluation in the proposed pipeline might also be too narrow. Throughout the paper, the authors discuss the stability of the polarised pattern, checked by an exhaustive search of the parameter space where the system reaches a steady state with a polarised pattern instead of a homogeneous pattern. It is not clear if the stability is related to the linear stability analysis of the reaction terms, as conducted in Goehring et al. (Science, 2011), which could indicate if a homogeneous state exists and whether it is stable or unstable. The stability test is performed through a pipeline procedure where they always start from a polarised pattern described by their model and observe how it evolves over time. It is unclear if the conclusions depend on the chosen initial conditions. Particularly, it is unclear what would happen if the initial distribution of posterior molecules is not exactly symmetric with respect to the anterior molecules, or if the initial polarisation is not strong.

We sincerely thank the editor(s) for the comment!

The definition of stability and its evaluation in the proposed pipeline consider two criteria: 1. The pattern is polarized; 2. The pattern is stable. Following simulations, figures, and videos (Fig. 1-6; Fig. S1-S5; Fig. S7-S9; Movie S1-S5) have sufficiently demonstrated that the parameters and networks set up capture the cell polarization dynamis regarding both the stable and unstable states very well.

Now we have added new simulation on alternative initial conditions. They demonstrating the necessity of a polarized initial pattern set up independently of the reaction-diffusion network during the establishment phase, probably through additional mechanisms such as the active actomyosin contractility and flow [Cuenca et al., Development, 2003; Gross et al., Nat. Phys., 2019]. Our conclusions ( i.e., single-sided self-regulation, single-sided additional regulation, and unequal system parameters cause the stable polarized pattern to collapse) have little dependence on the chosen initial conditions as long as the unsymmetric initial patterns can set up a stable polarized pattern. A part of the simulations institutively show our conclusions still hold if the initial distribution of posterior molecules is not exactly symmetric with respect to the anterior molecules, or if the initial polarisation is not strong (Fig. S4 and Fig. S9).

Regarding the biological interpretation and relevance of the model, it overlooks some important aspects of the C. elegans polarisation system. The authors focus solely on a reaction-diffusion formulation to reproduce the polarisation pattern. However, the polarisation of the C. elegans zygote consists of two distinct phases: establishment and maintenance, with actomyosin dynamics playing a crucial role in both phases (see Munro et al., Dev Cell 2004; Shivas & Skop, MBoC 2012; Liu et al., Dev Biol 2010; Wang et al., Nat Cell Biol 2017). Both myosin and actin are crucial to maintaining the localisation of PAR proteins during cell polarisation, yet the authors neglect cortical flows during the establishment phase and any effects driven by myosin and actin in their model, failing to capture the system's complexity. How this affects the proposed model and conclusions about the establishment of the polarisation pattern needs careful discussion. Additionally, they assume that diffusion in the cytoplasm is infinitely fast and that cytoplasmic flows do not play any role in cell polarity. Finite cytoplasmic diffusion combined with cytoplasmic flows could compromise the stability of the anterior-posterior molecular distributions. The authors claim that cytoplasmic diffusion coefficients are two orders of magnitude higher than membrane diffusion coefficients, but they seem to differ by only one order of magnitude (Petrášek et al., Biophys. J. 2008). The strength of cytoplasmic flows has been quantified by a few studies, including Cheeks et al., and Curr Biol 2004.

We sincerely thank the editor(s) for the comment!

Indeed, previous research highlighted the importance of convective cortical flow in orchestrating the localisation of PAR proteins during the establishment phase of polarisation formation [Goehring et al., J. Cell Biol., 2011; Rose et al., WormBook, 2014; Beatty et al., Development, 2013]. However, during the maintenance phase, the non-muscle myosin II (NMY-2) is regulated downstream by the PAR protein network rather than serving as the primary upstream factor controlling PAR protein localization [Goehring et al., J. Cell Biol., 2011; Rose et al., WormBook, 2014; Beatty et al., Development, 2013]. While some theoretical studies integrated both reaction-diffusion dynamics and the effects of myosin and actin [Tostevin, 2008; Goehring, Science, 2011], others focused exclusively on reaction-diffusion dynamics [Dawes et al., Biophys. J., 2011; Seirin-Lee et al., Cells, 2020]. We have now clarified the distinction between the establishment and maintenance phases in 1. Introduction, emphasized our research focus on the reaction-diffusion dynamics during the maintenance phase in 2. Results, and provided a discussion of the omitted actomyosin dynamics to foster a more comprehensive understanding in the future in 3. Discussion and conclusion. The effect of the establishment phase is studied as the initial condition for the cell polarization simulation solely governed by reaction-diffusion dynamics, with new simulations demonstrating the necessity of a polarized initial pattern set up independently of the reaction-diffusion network during the establishment phase, probably through additional mechanisms such as the active actomyosin contractility and flow [Cuenca et al., Development, 2003; Gross et al., Nat. Phys., 2019].

Cytoplasmic and membrane diffusion coefficients differ by two orders of magnitude according to previous experimental measurements on PAR-2 and PAR-6 [Goehring et al., J. Cell Biol., 2011; Lim et al., Cell Rep., 2021]. Many previous C. elegans cell polarization models have incorporated mass-conservation model combined with finite cytoplasmic diffusion, but this model description can lead to reverse spatial concentration distribution between the cell membrane and cytosol [Fig. 3 of Seirin-Lee et al., J. Theor. Biol., 2016; Fig. 2ab of Seirin-Lee et al., J. Math. Biol., 2020], disobeying experimental observation [Fig. 4A of Sailer et al., Dev. Cell, 2015; Fig. 1A of Lim et al., Cell Rep., 2021]. This implies that the infinite cytoplasmic diffusion, without precise experiment-based parameter assignment or accounting for other hidden biological processes ( e.g., protein production and degradation), may be inappropriate in modeling the real spatial concentration distributions distinguished between the cell membrane and cytosol. To address this issue, some theoretical research incorporated protein production and degradation into their model, to acquire the consistent spatial concentration distribution between the cell membrane and cytosol [Tostevin et al., Biophys. J., 2008]. More definitive experimental data on the spatiotemporal changes in protein diffusion, production, and degradation are essential for providing a more realistic representation of cellular dynamics and enhancing the model's predictive power.

Now we have acknowledged the possibly overlooked aspects of the C. elegans polarisation system in 3. Discussion and conclusion, a detailed outline of potential model improvements. Those aspects include, but are not limited to, issues involving “neglect cortical flows” and the “diffusion in the cytoplasm is infinitely fast”. From a theoretical perspective, we adopted assumptions from the previous literature and constructed a minimal model for a specific cell polarization phase to investigate the network's robustness. The meaningful predictions of five experimental groups and eight perturbed conditions in the C. elegans embryo faithfully supports the biological interpretation and relevance of the model.

Although the authors compare their model predictions to experimental observations, particularly in reproducing mutant behaviours, they do not explicitly show or discuss these comparisons in detail. Diffusion coefficients and off-rates for some PAR proteins have been measured (Goehring et al., JCB 2011), but the authors seem to use parameter values that differ by many orders of magnitude, perhaps due to applied scaling. To ensure meaningful predictions, whether their proposed model captures the extensive published data should be evaluated. Various cellular/genetic perturbations have been studied to understand their effects on anterior-posterior boundary positioning. Testing these perturbations' responses in the model would be important. For example, comparing the intensity distribution of PAR-6 and PAR-2 with measurements during the maintenance phase by Goehring et al., JCB 2011, or comparing the normalised intensity of PAR-3 and PKC-3 from the model with those measured by Wang et al., Nat Cell Biol 2017, during establishment and maintenance phases (in both wild-type and cdc-42 (RNAi) zygotes) could provide insightful validation. Additionally, in the presence of active CDC-42, it has been observed that PAR-6 extends further into the posterior side (Aceto et al., Dev Biol 2006). Conducting such validation tests is essential to convince readers that the model accurately represents the actual system and provides insights into pattern formation during cell polarisation.

We sincerely thank the editor(s) for the comment!

To provide more comprehensive validations and refinements to ensure the model accurately represents biological systems, we extensively reproduced the qualitative and semi-quantitative phenomenon in three more experimental groups previously published (Section 2.5; Fig. S8) [Gotta et al., Curr. Biol., 2001; Aceto et al., Dev. Biol., 2006]. Combined with the original experiments (Section 2.5; Fig. 5; Fig. S7) [Hoege et al., Curr. Biol., 2010; Beatty et al., Development, 2010; Beatty et al., Development, 2013], now we have reproduced five experimental groups in total from published data, comprising eight perturbed conditions and using wild-type as the reference. We have also explicitly show the comparison between model predictions and experimental observations (including the mutant behaviors reproduction as well) in detail, by describing how “cell polarization pattern characteristics in simulation” responds to various cellular/genetic perturbations (Section 2.5; Fig. 5; Fig. S7 and S8). The original and new validation tests conducted can convince readers that the model accurately represents the actual system and provides insights into pattern formation during cell polarisation.

The diffusion coefficients for anterior and posterior molecular species were assigned according to previous experimental and theoretical research [Goehring et al., J. Cell Biol., 2011; Goehring et al., Science, 2011; Seirin-Lee et al., Cells, 2020]. The off-rates are assigned uniformly by searching viable parameter sets that can set up a network with cell polarization pattern stability. Now we have added simulations showing that the cell polarization pattern stability and response to network structure and parameter perturbation does not depend on the exact parameter values (incl., diffusion coefficients and off-rates), provided the parameter values on both sides are initially balanced as a whole (Fig. S5). Specifically, we used a Monte Carlo method to sample a wide range of various parameter values ( i.e., γ, α, k₁, k₂, q₁, q₂ and [X_c) for all nodes and regulations in simple 2-node network and C. elegans 5-node network, to achieve pattern stability. Under these conditions ( i.e., without any reduction in the parameter space), single-sided self-regulation, single-sided additional regulation, and unequal system parameters still cause the stable polarized pattern to collapse, consistent with our conclusions in the simplified conditions with the parameter space reduced to three independent dimensions.

With the in silico time set as 2 sec per step, now we have added the Supplemental Text justifying how the units are removed during non-dimensionalization. This demonstrates that the derived non-dimensionalized parameter in this paper achieves realistic values on the same order of magnitude as those observed in reality, confirming the fidelity of the proposed model in representing the real system. We agreed that full experimental measurements of biological information are essential for establishing a more utilizable model and discussed it thoroughly in 3. Discussion and conclusion.

A clear justification, with references, for each network interaction between nodes in the five-node model is needed. Some of the activatory/inhibitory signals proposed by the authors have not been demonstrated ( e.g. CDC-42 directly inhibiting CHIN-1). Table S2 provided by the authors is insufficient to justify each node-node interaction, requiring additional explanations. (See the review by Gubieda et al., Phil. Trans. R. Soc. B 2020, for a similar node network that differs from the authors' model.) Additionally, the intensity distributions of cortical PAR-3 and PKC-3 seem to vary significantly during both establishment and maintenance phases (Wang et al., Nat Cell Biol 2017), yet the authors consider the PAR-3/PAR-6/PKC-3 as a single complex. The choices in the model should be justified, as the presence or absence of clustering of these PAR proteins can be crucial during cell polarisation (Wang et al., Nat Cell Biol 2017; Dawes & Munro, Biophys J 2011).

We sincerely thank the editor(s) for the comment!

Now we have acknowledged the limitations of the current cell polarization model and provided, in 2. Results and 3. Discussion and conclusion, a detailed outline of potential model improvements. The limitations include, but are not limited to, issues involving “each network interaction between nodes” and the “consider the PAR-3/PAR-6/PKC-3 as a single complex”, in which the former one relies on experimental measurements of biological information. However, comprehensive experimental measurement data on every molecular species, their interactions, and each species’ intensity distribution in space and time were not fully available from prior research. Refinement is lacking for some of these interactions, potentially requiring years of additional experimentation. Moreover, for certain species at specific developmental stages, only relative (rather than absolute) intensity measurements are available. We agreed that such information is essential for establishing a more utilizable model and discussed it thoroughly in 3. Discussion and conclusion.

In consistent with previous modeling efforts [Goehring et al., Science, 2011; Gross et al., Nat. Phys., 2019; Lim et al., Cell Rep., 2021], our model treats the PAR-3/PAR-6/PKC-3 complex as a single entity for simplification, thus neglecting the potentially distinct spatial distributions of each single molecular species. We agree that a more comprehensive model, capable of resolving the individual localization patterns of these anterior PAR proteins, would be a valuable future direction. From a theoretical perspective, we adopted assumptions from the previous literature and constructed a minimal model for a specific cell polarization phase to investigate the network's robustness, supported by five experimental groups and eight perturbed conditions in the C. elegans embryo.

In summary, the authors successfully demonstrate the importance of compensatory actions in maintaining polarisation robustness. Their computational pipeline offers valuable insights into the dynamics of reaction-diffusion networks. However, the lack of detailed experimental validation and realistic parameter estimation limits the model's applicability to real biological systems. While the study provides a solid foundation, further work is needed to fully characterise and validate the model in natural contexts. This work has the potential to significantly impact the field by providing a new perspective on the robustness of cell polarisation networks.

We sincerely thank the editor(s) for the pertinent summary!

To provide a more comprehensive validation against experimental data and model parameters, three more groups of the qualitative and semi-quantitative phenomenon regarding CDC-42 are reproduced based on previously published experiments (Section 2.5; Fig. S8) [Gotta et al., Curr. Biol., 2001; Aceto et al., Dev. Biol., 2006]. Combined with the original experiments (Section 2.5; Fig. 5; Fig. S7) [Hoege et al., Curr. Biol., 2010; Beatty et al., Development, 2010; Beatty et al., Development, 2013], now we have reproduced five experimental groups in total, comprising eight perturbed conditions and using wild-type as the reference.

With the in silico time set as 2 sec per step, now we have added the Supplemental Text justifying how the units are removed during non-dimensionalization. This demonstrates that the derived non-dimensionalized parameter in this paper achieves realistic values on the same order of magnitude as those observed in reality, confirming the fidelity of the proposed model in representing the real system. Together with the reproduction of five experimental groups (eight perturbed conditions with wild-type as the reference), the model’s applicability to real biological systems in natural contexts are are fully characterised and validated.

The computational pipeline developed could be a valuable tool for further in silico experiments, allowing researchers to explore the dynamics of more complex networks. To maximise its utility, the model needs comprehensive validation and refinement to ensure it accurately represents biological systems. Addressing these limitations, particularly the need for more detailed experimental validation and realistic parameter choices, will enhance the model's predictive power and its applicability to understanding cell polarisation in natural systems.

We sincerely thank the editor(s) for the comment!

To provide more comprehensive validations and refinements to ensure the model accurately represents biological systems, we extensively reproduced the qualitative and semi-quantitative phenomenon in three more experimental groups previously published (Section 2.5; Fig. S8) [Gotta et al., Curr. Biol., 2001; Aceto et al., Dev. Biol., 2006]. Combined with the original experiments (Section 2.5; Fig. 5; Fig. S7) [Hoege et al., Curr. Biol., 2010; Beatty et al., Development, 2010; Beatty et al., Development, 2013], now we have reproduced five experimental groups in total from published data, comprising eight perturbed conditions and using wild-type as the reference. We have also explicitly show the comparison between model predictions and experimental observations (including the mutant behaviors reproduction as well) in detail, by describing how “cell polarization pattern characteristics in simulation” responds to various cellular/genetic perturbations (Section 2.5; Fig. 5; Fig. S7 and S8).

With the in silico time set as 2 sec per step, now we have added the Supplemental Text justifying how the units are removed during non-dimensionalization. This demonstrates that the derived non-dimensionalized parameter in this paper achieves realistic values on the same order of magnitude as those observed in reality, confirming the fidelity of the proposed model in representing the real system. Together with the reproduction of five experimental groups (eight perturbed conditions with wild-type as the reference), the model's predictive power and its applicability to understanding cell polarisation in natural systems are enhanced.

Now we have added simulations showing that the cell polarization pattern stability and response to network structure and parameter perturbation does not depend on the exact parameter values (incl., diffusion coefficients, basal off-rates and inhibition intensity), provided the parameter values on both sides are initially balanced as a whole (Fig. S5). Specifically, we used a Monte Carlo method to sample a wide range of various parameter values (i.e., γ, α, k₁, k₂, q₁, q₂ and [X_c) for all nodes and regulations in simple 2-node network and C. elegans 5-node network, to achieve pattern stability. Under these conditions ( i.e., without any reduction in the parameter space), single-sided self-regulation, single-sided additional regulation, and unequal system parameters still cause the stable polarized pattern to collapse, consistent with our conclusions in the simplified conditions with the parameter space reduced to three independent dimensions.

Recommendations for the Authors:

(1) Parameterisation and Model Validation: The authors utilise parameter values that lack realism and fail to provide units for some of them, which can lead to confusion. For instance, the length of the cell is set to 0.5 without clear justification, raising questions about the scale used. Additionally, there's a mix of dimensional and non-dimensional variables, potentially complicating interpretation. Furthermore, arbitrary choices such as equal Hill coefficients and setting inhibition intensity parameters to 1 raise concerns about model fidelity. To ensure meaningful predictions, the authors should validate their model against extensive published data, including cellular/genetic perturbations. For example, comparing intensity distributions of PAR proteins measured during maintenance phases by Goehring et al., JCB 2011, and those obtained from the model could provide valuable validation. Similarly, comparisons with data from Wang et al., Nat Cell Biol 2017, on wild-type and cdc-42 (RNAi) zygotes, as well as observations from Aceto et al., Dev Biol 2006, on PAR-6 extension in the presence of active CDC-42, would strengthen the model's validity. Such validation tests are essential for convincing readers that the model accurately represents the actual system and can provide insights into pattern formation during cell polarisation.

We sincerely thank the editor(s) and referee(s) for the helpful suggestion!

Now we have added a new section, Parameter Nondimensionalization and Order of Magtitude Consistency, into Supplemental Text. In this section, we introduced how we adopted the parameter nondimensionalization and value assignments from previous works [Goehring et al., J. Cell Biol., 2011; Goehring et al., Science, 2011; Seirin-Lee et al., Cells, 2020]. We listed four examples (i.e., evolution time, membrane diffusion coefficient, basal off-rate, and inhibition intensity) to show the consistency in order of magtitude between numerical and realistic values.

The assumption of “equal Hill coefficients” is to reduce the parameter space for an affordable computational cost. It is a widely-used strategy to fix Hill coefficients [Seirin-Lee et al., J. Theor. Biol., 2015; Seirin-Lee, Bull. Math. Biol., 2021] in network research, to control computational cost. Besides, setting inhibition intensity parameters to 1 is for determining a numerical scale. Now we have added simulations showing that the cell polarization pattern stability does not depend on the exact parameter values associated with activation and inhibition pathways, provided the regulations on both sides are initially balanced as a whole (Fig. S5). Specifically, we used a Monte Carlo method to sample a wide range of various parameter values (i.e., γ, α, k₁, k₂, q₁, q₂ and [X_c) for all nodes and regulations in simple 2-node network and C. elegans 5-node network, to achieve pattern stability. Under these conditions (i.e., without any reduction in the parameter space), single-sided self-regulation, single-sided additional regulation, and unequal system parameters still cause the stable polarized pattern to collapse, consistent with our conclusions in the simplified conditions with the parameter space reduced to three independent dimensions.

To confirm the fidelity of the proposed model in representing the real system, we reproduced the qualitative and semi-quantitative phenomenon in three more experimental groups previously published (Section 2.5; Fig. S8) [Gotta et al., Curr. Biol., 2001; Aceto et al., Dev. Biol., 2006]. Combined with the original experiments (Section 2.5; Fig. 5; Fig. S7) [Hoege et al., Curr. Biol., 2010; Beatty et al., Development, 2010; Beatty et al., Development, 2013], now we have reproduced five experimental groups in total (two acting on LGL-1 and three on CDC-42), comprising eight perturbed conditions and using wild-type as the reference. These results effectively demonstrate how comprehensively the network structure and parameters capture the characteristics of the C. elegans embryo. We have also acknowledged the limitations of the current cell polarization model and provided, in 2. Results and 3. Discussion and conclusion, a detailed outline of potential model improvements.

It is worth noting that, although a strict match between numerical and realistic parameter values with consistent units is always helpful, a lot of notable pure numerical studies successfully unveil principles that help interpret [Ma et al., Cell, 2009] and synthesize real biological systems [Chau et al., Cell, 2012]. These studies suggest that numerical analysis in biological systems remains powerful, even when comprehensive experimental data from prior research are not fully available.

(2) Parameter Changes: It is not clear how the parameters change as more complicated networks are explored, and how this affects the comparison between the simple and complete model. Clarification on this point would be beneficial.

We sincerely thank the editor(s) and referee(s) for the helpful suggestion!

The computational pipeline in Section 2.1 is generalized for all reaction-diffusion networks, including the simple and complete ones studied in this paper. The parameter changes included two parts: 1. The mutual activation in the anterior (none for the simple 2-node network and q<sub2</sub> for the complete 5-node network); 2. The viable parameter sets (122 sets for the simple 2-node network and 602 sets for the complete 5-node network). Now we have explicitly clarified those differences:

Those differences don’t affect the comparison between the simple and complete models. Now we have added comprehensive comparisons between the simple and complete models about 1. How they respond to alternative initial conditions consistently (Fig. S2). 2. How they respond to alternative single modifications consistently (Fig. S4 and S9), even when the parameters (i.e., γ, α, k₁, k₂, q₁, q₂ and [X_c) are assigned with various values concerning all nodes and regulations (Fig. S5).

(3) Exploration of Model Parameter Space: In the two-node dual antagonistic model, the authors observe that the cell polarisation pattern is unstable for different systems (Fig. 1). However, it remains uncertain whether this instability holds true for the entire model parameter space. Have the authors thoroughly screened the full model parameter space to support their statements? It would be beneficial for the authors to provide clarification on the extent of their exploration of the model parameter space to ensure the robustness of their conclusions.

We sincerely thank the editor(s) and referee(s) for the helpful suggestion!

The trade-off between considered parameter space and computational cost is a long-term challenge in network study as there are always numerous combinations of network nodes, edges, and parameters [Ma et al., Cell, 2009; Chau et al., Cell, 2012]. The computational pipeline in Section 2.1 generalized for all reaction-diffusion networks exerts two strategies to limit the computational cost and set up a basic network reference: 1. Dimension Reduction (Strategy 1) - Unifying the parameter values for different nodes and different edges within the same regulatory type to minimize the unidentical parameter numbers into 3; 2: Parameter Space Confinement (Strategy 2): Enumerating the dimensionless parameter set on a three-dimensional (3D) grid confined by γ∈ [0,0.05] in steps ∆γ = 0.001, k₁∈[0,5] in steps ∆k₁ = 0.05,  and  in steps .

In the early stage of our project, we tried to explore “the entire model parameter space” as indicated by the reviewer. We first tried to use the Monte Carlo method to find parameter solutions in an open parameter space and with all parameter values allowed to be different. However, such a process is full of randomness and is computationally expensive (taking months to search viable parameter sets but still unable to profile the continuous viable parameter space; the probability of finding a viable parameter set is no higher than 0.02%, making it very hard to profile a continuous viable parameter space). Now we clearly can see the viable parameter space is a thin curved surface where all parameters have to satisfy a critical balance (Fig. 3a, b, Fig. 5e, f). This is why we exert a typical strategy for dimension reduction in network research in both cell polarization [Marée et al., Bull. Math. Biol., 2006; Goehring et al., Science, 2011; Trong et al., New J. Phys., 2014] and other biological topics (e.g., plasmid transferring in the microbial community [Wang et al., Nat. Commun., 2020]), i.e., unifying the parameter values for different nodes and different edges within the same regulatory type.

Additionally, the curved surface for viable parameter space can be extended to infinite as long as the parameter balance is achieved (Fig. 3a, b, Fig. 5e, f), it is impossible or unnecessary to explore “the entire model parameter space”. Setting up a confined parameter region near the original point for parameter enumeration can help profile the continuous viable parameter space, which is sufficient for presenting the central conclusion of this paper – that is - the network structure and parameter need to satisfy a balance for stable cell polarization.

To support a comprehensive study considering all kinds of reference and perturbed networks, we have maximized the parameter domain size by exhausting all the computational research we can access, including 400-500 Intel(R) Core(TM) E5-2670v2 and Gold 6132 CPU on the server (High-Performance Computing Platform at Peking University) and 5 Intel(R) Core(TM) i9-14900HX CPU on personal computers.

To make it certain that instability holds true when the model parameter space is extended, we add a comprehensive comparison between the simple and complete models about how their instability occurs consistently even when the parameters (i.e., γ, α, k₁, k₂, q₁, q₂ and [X_c) are assigned with various values concerning all nodes and regulations, searched by the Monte Carlo method (Fig. S5).

(4) Sensitivity of Numerical Solutions to Initial Conditions: Are the numerical solutions in both models sensitive to the chosen initial condition? What results do the models provide if uniform initial distributions were utilised instead?

We sincerely thank the editor(s) and referee(s) for the comments!

To investigate both the simple network and the realistic network consisting of various node numbers and regulatory pathways [Goehring et al., Science, 2011; Lang et al., Development, 2017], we propose a computational pipeline for numerical exploration of the dynamics of a given reaction-diffusion network's dynamics, specifically targeting the maintenance phase of stable cell polarization after its initial establishment [Motegi et al., Nat. Cell Biol., 2011; Goehring et al., Science, 2011; Seirin-Lee et al., Cells, 2020].

Now we have added new simulations and explanations for the sensitivity of numerical solutions to initial conditions. For both models, a uniform initial distribution leads to a homogeneous pattern while a Gaussian noise distribution leads to a multipolar pattern. In contrast, an initial polarized distribution (even with shifts in transition planes, weak polarization, or asymmetric curve shapes between the two molecular species) can maintain cell polarization reliably.

(5) Initial Conditions and Stability Tests: In Figure 1, the authors discuss the stability of the basic two-node network (a) upon modifications in (b-d). The stability test is performed through a pipeline procedure in which they always start from a polarised pattern described by Equation (4) and observe how the pattern evolves over time. It would be beneficial to explore whether the stability test depends on this specific initial condition. For instance, what would happen if the posterior molecules have an initial distribution of 1/(1+e^(-10x)), which is not exactly symmetric with respect to the anterior molecules' distribution of 1-1/(1+e^(-20x))? Additionally, if the initial polarisation is not as strong, for example, with the anterior molecules having a distribution of 10-1/(1+e^(-20x)) and the posterior molecules having a distribution of 9+1/(1+e^(-20x)), how would this affect the results?

We sincerely thank the editor(s) and referee(s) for the constructive advice!

Now we have added comprehensive comparisons between the simple and complete models about how they respond to alternative initial conditions consistently (Fig. S4, Fig. S9). The successful cell polarization pattern requests an initial polarized pattern, but its following stability and response to perturbation depend very little on the specific form of the initial polarized pattern. All the conditions mentioned by the reviewer have been included.

(6) Stability Analysis: Throughout the paper, the authors discuss the stability of the polarised pattern. The stability is checked by an exhaustive search of the parameter space, ensuring the system reaches a steady state with a polarised pattern instead of a homogeneous pattern. It would be beneficial to explore if this stability is related to a linear stability analysis of the model parameters, similar to what was conducted in Reference [18], which can determine if a homogeneous state exists and whether it is stable or unstable. Including such an analysis could provide deeper insights into the system's stability and validate its robustness.

We sincerely thank the editor(s) and referee(s) for the comments!

We agree that the linear stability analysis can potentially offer additional insights into polarized pattern behavior. However, this approach often requests the aid of numerical solutions and is therefore not entirely independent [Goehring et al., Science, 2011]. Over the past decade, numerical simulations have consistently proven to be a reliable and sufficient approach for studying network dynamics, spanning from C. elegans cell polarization [Tostevin et al., Biophys. J, 2008; Blanchoud et al., Biophys. J, 2015; Seirin-Lee, Dev. Growth Differ., 2020] to topics in metazoon [Chau et al., Cell, 2012; Qiao et al., eLife, 2022; Sokolowski et al., arXiv, 2023]. Numerous purely numerical studies have successfully unveiled principles that help interpret [Ma et al., Cell, 2009] and synthesized real biological systems [Chau et al., Cell, 2012], independent of additional mathematical analysis. Thus, we leverage our numerical framework to address the cell polarization problems cell polarization problems in this paper.

To confirm the reliability of stability checked by an exhaustive search of the parameter space, now we reproduce the qualitative and semi-quantitative phenomenon in three more experimental groups previously published (Section 2.5; Fig. S8) [Gotta et al., Curr. Biol., 2001; Aceto et al., Dev. Biol., 2006]. Combined with the original experiments (Section 2.5; Fig. 5; Fig. S7) [Hoege et al., Curr. Biol., 2010; Beatty et al., Development, 2010; Beatty et al., Development, 2013], we reproduce five experimental groups in total (two acting on LGL-1 and three acting on CDC-42), comprising eight perturbed conditions and using wild-type as the reference.

To confirm the robustness of our conclusions regarding the system's stability, now we add comprehensive comparisons between the simple and complete models about 1. How they respond to alternative initial conditions consistently (Fig. S4; Fig. S9). 2. How they respond to alternative single modifications consistently, even when the parameters (i.e., γ, α, k₁, k₂, q₁, q₂ and [X_c ) are assigned with various values concerning all nodes and regulations (Fig. S5).

(7) Interface Position Determination: In Figure 4, the authors demonstrate that by using a spatially varied parameter, the position of the interface can be tuned. Particularly, the interface is almost located at the step where the parameter has a sharp jump. However, in the case of a homogeneous parameter (e.g., Figure 4(a)), the system also reaches a stable polarised pattern with the interface located in the middle (x = 0), similar to Figure 4(b), even though the homogeneous parameter does not contain any positional information of the interface. It would be helpful to clarify the difference between Figure 4(a) and Figure 4(b) in terms of the interface position determination.

We sincerely thank the editor(s) and referee(s) for the comments!

The case of a homogeneous parameter (e.g., Fig. 4a), in which the system also reaches a stable polarised pattern with the interface located in the middle (x = 0), is just a reference adopted from Fig. 1a to show that the inhomogeneous positional information in Fig. 4b can achieve a similar stable polarised pattern.

Now we clarify the interface position determination to Section 2.4 to improve readability. Moreover, it is marked with grey dashed line in all the patterns in Fig. 4 and Fig. 6 to highlight the importance of inhomogeneous parameters on interface localization.

(8) Presented Comparison with Experimental Observations: The comparison with experimental observations lacks clarity. It isn't clear that the model "faithfully recapitulates" the experimental observations (lines 369-370). We recommend discussing and showing these comparisons more carefully, highlighting the expectations and similarities.

We sincerely thank the editor(s) and referee(s) for the constructive suggestion!

Now we remove the word “faithfully” and highlight the expectations and similarities of each experimental group by describing “cell polarization pattern characteristics in simulation: …”.

(9) Validation of Model with Experimental Data: Given the extensive number of model parameters and the uncertainty of their values, it is essential for the authors to validate their model by comparing their results with experimental data. While C. elegans polarisation has been extensively studied, the authors have yet to utilise existing data for parameter estimation and model validation. Doing so would considerably strengthen their study.

We sincerely thank the editor(s) and referee(s) for the constructive suggestion!

To utilise existing data for parameter estimation, now we add a new section, Parameter Nondimensionalization and Order of Magtitude Consistency, into Supplemental Text. In this section, we introduced how we adopted the parameter nondimensionalization and value assignments from previous works [Goehring et al., J. Cell Biol., 2011; Goehring et al., Science, 2011; Seirin-Lee et al., Cells, 2020]. We listed four examples (i.e., evolution time, membrane diffusion coefficient, basal off-rate, and inhibition intensity) to show the consistency in order of magtitude between numerical and realistic values.

To utilise existing data for model validation, now we reproduce the qualitative and semi-quantitative phenomenon in three more experimental groups previously published (Section 2.5; Fig. S8) [Gotta et al., Curr. Biol., 2001; Aceto et al., Dev. Biol., 2006]. Combined with the original experiments (Section 2.5; Fig. 5; Fig. S7) [Hoege et al., Curr. Biol., 2010; Beatty et al., Development, 2010; Beatty et al., Development, 2013], we reproduce five experimental groups in total (two acting on LGL-1 and three acting on CDC-42), comprising eight perturbed conditions and using wild-type as the reference.

Also, we acknowledge the limitations of the current cell polarization model and provided, in 3. Discussion and conclusion, a detailed outline of potential model improvements. The limitations include, but are not limited to, issues involving “extensive number of model parameters” and “uncertainty of their values”, both of which rely on experimental measurements of biological information. However, comprehensive experimental measurement data on every molecular species, their interactions, and each species’ intensity distribution in space and time were not fully available from prior research. Refinement is lacking for some of these interactions, potentially requiring years of additional experimentation. Moreover, for certain species at specific developmental stages, only relative (rather than absolute) intensity measurements are available. We agreed that such information is essential for establishing a more utilizable model and discussed it thoroughly in 3. Discussion and conclusion. From a theoretical perspective, we adopted assumptions from the previous literature and constructed a minimal model for a specific cell polarization phase to investigate the network's robustness, supported by five experimental groups and eight perturbed conditions with wild-type as a reference in the C. elegans embryo.

(10) Enhancing Model Accuracy by Considering Cortical Flows: The authors are encouraged to include cortical flows in their cell polarisation model, as these flows are known to be pivotal in the process. Although the current model successfully predicts cell polarisation without accounting for cortical flows, research has demonstrated their significant role in polarisation formation. By incorporating cortical flows, the model would provide a more thorough and precise representation of the biological process. Furthermore, previous studies, such as those by Goehring et al. (References 17 and 18), highlight the importance of convective actin flow in initiating polarisation. It would be valuable for the authors to address the contribution of convection with actin flow to the establishment of the polarisation pattern. The polarisation of the C. elegans zygote progresses through two distinct phases: establishment and maintenance, both heavily influenced by actomyosin dynamics. Works by Munro et al. (Dev Cell 2004), Shivas & Skop (MBoC 2012), Liu et al. (Dev. Biol. 2010), and Wang et al. (Nat Cell Biol 2017) underscore the critical roles of myosin and actin in orchestrating the localisation of PAR proteins during cell polarisation. To enhance the fidelity of their model, we recommend that the authors either integrate cortical flows and consider the effects driven by myosin and actin, or provide a discussion on the repercussions of omitting these dynamics.

We sincerely thank the editor(s) and referee(s) for the comment!

Indeed, previous research highlighted the importance of convective cortical flow in orchestrating the localisation of PAR proteins during the establishment phase of polarisation formation [Goehring et al., J. Cell Biol., 2011; Rose et al., WormBook, 2014; Beatty et al., Development, 2013]. However, during the maintenance phase, the non-muscle myosin II (NMY-2) is regulated downstream by the PAR protein network rather than serving as the primary upstream factor controlling PAR protein localization. While some theoretical studies integrated both reaction-diffusion dynamics and the effects of myosin and actin [Tostevin et al., Biophys J, 2008; Goehring et al, Science, 2011], others focused exclusively on reaction-diffusion dynamics [Dawes et al., Biophys. J., 2011; Seirin-Lee et al., Cells, 2020]. Now we clarify the distinction between the establishment and maintenance phases, emphasize our research focus on the reaction-diffusion dynamics during the maintenance phase, and provide a discussion of these omitted dynamics to foster a more comprehensive understanding in the future, as suggested.

(11) Further Justification of Network Interactions: The authors should provide additional explanations, supported by empirical evidence, for the network interactions assumed in their model. This includes both node-node interactions and the rationale behind protein complex formations. Some of the proposed interactions lack empirical validation, as noted in studies such as Gubieda et al., Phil. Trans. R. Soc. B 2020. Additionally, discrepancies in protein intensity distributions, as observed in Wang et al., Nat Cell Biol 2017, should be addressed, particularly concerning the consideration of the PAR-3/PAR-6/PKC-3 complex as a single entity. Justifying these choices is crucial for ensuring the model's credibility and alignment with experimental findings.

We sincerely thank the editor(s) and referee(s) for the helpful advice!

In consistency with previous modeling efforts [Goehring et al., Science, 2011; Gross et al., Nat. Phys., 2019; Lim et al., Cell Rep., 2021], our model treats the PAR-3/PAR-6/PKC-3 complex as a single entity for simplification, thus neglecting the potentially distinct spatial distributions of each single molecular species.

Now we acknowledge the limitations of the current cell polarization model and provided, in 3. Discussion and conclusion, a detailed outline of potential model improvements. The limitations include, but are not limited to, issues involving “node-node interactions” and “discrepancies in protein intensity distributions”, both of which rely on experimental measurements of biological information. However, comprehensive experimental measurement data on every molecular species, their interactions, and each species’ intensity distribution in space and time were not fully available from prior research. Refinement is lacking for some of these interactions, potentially requiring years of additional experimentation. Moreover, for certain species at specific developmental stages, only relative (rather than absolute) intensity measurements are available. We agreed that such information is essential for establishing a more utilizable model and discussed it thoroughly in 3. Discussion and conclusion.

To ensure the model's credibility and alignment with experimental findings, now we reproduce the qualitative and semi-quantitative phenomenon in three more experimental groups previously published (Section 2.5; Fig. S8) [Gotta et al., Curr. Biol., 2001; Aceto et al., Dev. Biol., 2006]. Combined with the original experiments (Section 2.5; Fig. 5; Fig. S7) [Hoege et al., Curr. Biol., 2010; Beatty et al., Development, 2010; Beatty et al., Development, 2013], now we have reproduced five experimental groups in total (two acting on LGL-1 and three on CDC-42), comprising eight perturbed conditions and using wild-type as the reference.

(12) Further Justification of Node-Node Network Interactions: The authors should provide further justification for the node-node network interactions assumed in their study. To the best of our knowledge, some of the node-node interactions proposed have not yet been empirically demonstrated. Providing additional explanations for these interactions would enhance the credibility of the model and ensure its alignment with empirical evidence.

We sincerely thank the editor(s) and referee(s) for the helpful advice!

Now we acknowledge the limitations of the current cell polarization model and provided, in 3. Discussion and conclusion, a detailed outline of potential model improvements. The limitations include, but are not limited to, issues involving “node-node network interactions”, which rely on experimental measurements of biological information. However, comprehensive experimental measurement data on every molecular species, their interactions, and each species’ intensity distribution in space and time were not fully available from prior research. Refinement is lacking for some of these interactions, potentially requiring years of additional experimentation. Moreover, for certain species at specific developmental stages, only relative (rather than absolute) intensity measurements are available. We agreed that such information is essential for establishing a more utilizable model and discussed it thoroughly in 3. Discussion and conclusion.

To enhance the credibility of the model and ensure its alignment with empirical evidence, we reproduced the qualitative and semi-quantitative phenomenon in three more experimental groups previously published (Section 2.5; Fig. S8) [Gotta et al., Curr. Biol., 2001; Aceto et al., Dev. Biol., 2006]. Combined with the original experiments (Section 2.5; Fig. 5; Fig. S7) [Hoege et al., Curr. Biol., 2010; Beatty et al., Development, 2010; Beatty et al., Development, 2013], now we have reproduced five experimental groups in total (two acting on LGL-1 and three on CDC-42), comprising eight perturbed conditions and using wild-type as the reference.

(13) Justification for Network Interactions and Protein Complexes: The authors must provide clear justifications, supported by references, for each network interaction between nodes in the five-node model. Some of the activatory/inhibitory signals proposed lack empirical validation, such as CDC-42 directly inhibiting CHIN-1. The provided Table S2 is insufficient to justify these interactions, necessitating additional explanations. Reviewing relevant literature, such as the work by Gubieda et al., Phil. Trans. R. Soc. B 2020, may offer insights into similar node networks. Furthermore, the authors should address discrepancies in protein intensity distributions, as observed in studies like Wang et al., Nat Cell Biol 2017. Specifically, the authors consider the PAR-3/PAR-6/PKC-3 complex as a single entity despite potential differences in their distributions. Justification for this choice is essential, particularly considering the importance of clustering dynamics during cell polarisation, as demonstrated by Wang et al., Nat Cell Biol 2017, and Dawes & Munro, Biophys J 2011.

We sincerely thank the editor(s) and referee(s) for the helpful advice!

In consistent with previous modeling efforts [Goehring et al., Science, 2011; Gross et al., Nat. Phys., 2019; Lim et al., Cell Rep., 2021], our model treats the PAR-3/PAR-6/PKC-3 complex as a single entity for simplification, thus neglecting the potentially distinct spatial distributions of each single molecular species. Besides, the inhibition of CHIN-1 from CDC-42, which recruits cytoplasmic PAR-6/PKC-3 to form a complex, may act indirectly to restrict CHIN-1 localization through phosphorylation [Sailer et al., Dev. Cell, 2015; Lang et al., Development, 2017].

Now we acknowledge the limitations of the current cell polarization model and provided, in 3. Discussion and conclusion, a detailed outline of potential model improvements. The limitations include, but are not limited to, issues involving “each network interaction between nodes in the five-node model” and “discrepancies in protein intensity distributions”, both of which rely on experimental measurements of biological information. However, comprehensive experimental measurement data on every molecular species, their interactions, and each species’ intensity distribution in space and time were not fully available from prior research. Refinement is lacking for some of these interactions, potentially requiring years of additional experimentation. Moreover, for certain species at specific developmental stages, only relative (rather than absolute) intensity measurements are available. We agreed that such information is essential for establishing a more utilizable model and discussed it thoroughly in 3. Discussion and conclusion. From a theoretical perspective, we adopted assumptions from the previous literature and constructed a minimal model for a specific cell polarization phase to investigate the network's robustness, supported by five experimental groups and eight perturbed conditions with wild-type as a reference in the C. elegans embryo.

(14) Incorporating Cytoplasmic Dynamics into the Model: The authors assume infinite cytoplasmic diffusion and neglect the role of cytoplasmic flows in cell polarity, which may oversimplify the model. Finite cytoplasmic diffusion combined with flows could potentially compromise the stability of anterior-posterior molecular distributions, affecting the accuracy of the model's predictions. The authors claim a significant difference between cytoplasmic and membrane diffusion coefficients, but the actual disparity seems smaller based on data from Petrášek et al., Biophys. J. 2008. For example, cytosolic diffusion coefficients for NMY-2 and PAR-2 differ by less than one order of magnitude. Additionally, the strength of cytoplasmic flows, as quantified by studies such as Cheeks et al., and Curr Biol 2004, should be considered when assessing the impact of cytoplasmic dynamics on polarity stability. Incorporating finite cytoplasmic diffusion and cytoplasmic flows into the model could provide a more realistic representation of cellular dynamics and enhance the model's predictive power.

We sincerely thank the editor(s) and referee(s) for the comment!

Cytoplasmic and membrane diffusion coefficients differ by two orders of magnitude according to previous experimental measurements on PAR-2 and PAR-6 [Goehring et al., J. Cell Biol., 2011; Lim et al., Cell Rep., 2021]. Many previous C. elegans cell polarization models have incorporated mass-conservation model combined with finite cytoplasmic diffusion, but this model description can lead to reverse spatial concentration distribution between the cell membrane and cytosol [Fig. 3 of Seirin-Lee et al., J. Theor. Biol., 2016; Fig. 2ab of Seirin-Lee et al., J. Math. Biol., 2020], disobeying experimental observation [Fig. 4A of Sailer et al., Dev. Cell, 2015; Fig. 1A of Lim et al., Cell Rep., 2021]. This implies that the infinite cytoplasmic diffusion, without precise experiment-based parameter assignment or accounting for other hidden biological processes (e.g., protein production and degradation), may be inappropriate in modeling the real spatial concentration distributions distinguished between the cell membrane and cytosol. To address this issue, some theoretical research incorporated protein production and degradation into their model, to acquire the consistent spatial concentration distribution between the cell membrane and cytosol [Tostevin et al., Biophys. J., 2008]. More definitive experimental data on the spatiotemporal changes in protein diffusion, production, and degradation are essential for providing a more realistic representation of cellular dynamics and enhancing the model's predictive power.

Cytoplasmic flows indeed play an unneglectable role in cell polarity during the establishment phase [Kravtsova et al., Bull. Math. Biol., 2014], which creates a spatial gradient of actomyosin contractility and directs PAR-3/PKC-3/PAR-6 to the anterior membrane by cortical flow [Rose et al., WormBook, 2014; Lang et al., Development, 2017]. However, during the maintenance phase, the non-muscle myosin II (NMY-2) is regulated downstream by the PAR protein network rather than serving as the primary upstream factor controlling PAR protein localization [Goehring et al., J. Cell Biol., 2011; Rose et al., WormBook, 2014; Geβele et al., Nat. Commun., 2020]. While some theoretical studies integrated both reaction-diffusion dynamics and the effects of myosin and actin [Tostevin, 2008; Goehring, Science, 2011], others focused exclusively on reaction-diffusion dynamics [Dawes et al., Biophys. J., 2011; Seirin-Lee et al., Cells, 2020]. We now emphasize our research focus on the reaction-diffusion dynamics during the maintenance phase, so the dynamics between NMY-2 and PAR-2 are not included. We have also provided a discussion of the simplified cytoplasmic diffusion and omitted cytoplasmic flows to foster a more comprehensive understanding in the future.

(15) Explanation of Lethality References: On page 13, the authors mention lethality without adequately explaining why they are drawing connections with lethality experimental data.

We sincerely thank the editor(s) and referee(s) for the comment!

It is well-known that cell polarity loss in C. elegans zygote will lead to symmetric cell division, which brings out the more symmetric allocation of molecular-to-cellular contents in daughter cells; this will result in abnormal cell size, cell cycle length, and cell fate in daughter cells, followed by embryo lethality [Beatty et al., Development, 2010; Beatty et al., Development, 2013; Rodriguez et al., Dev. Cell, 2017; Jankele et al., eLife, 2021]. Now we explain why we are drawing connections with lethality experimental data in Section 2.5.

(16) Improved Abstract: "...However, polarity can be restored through a combination of two modifications that have opposing effects..." This sentence could be revised for better clarity. For example, the authors could consider rephrasing it as follows: "...However, polarity restoration can be achieved by combining two modifications with opposing effects...".

We sincerely thank the editor(s) and referee(s) for helpful advice!

Now we revise the abstract as follows:

“Abstract – However, polarity restoration can be achieved by combining two modifications with opposing effects.”

(17) Conservation of Mass in Network Models: Is conservation of mass satisfied in their network models?

We sincerely thank the editor (s) and referee(s) for the comment!

While previous experiments provide evidence for near-constant protein mass during the establishment phase [Goehring et al., Science, 2011], whether this is consistent until the end of maintenance is unclear.

Many previous C. elegans cell polarization models have assumed mass conservation on the cell membrane and in the cell cytosol, this model description can lead to reverse spatial concentration distribution between the cell membrane and cytosol [Fig. 3 of Seirin-Lee et al., J. Theor. Biol., 2016; Fig. 2ab of Seirin-Lee et al., J. Math. Biol., 2020], disobeying experimental observation [Fig. 4A of Sailer et al., Dev. Cell, 2015; Fig. 1A of Lim et al., Cell Rep., 2021]. This implies that mass conservation may be inappropriate in modeling the real spatial concentration distributions distinguished between the cell membrane and cytosol. To address this issue, some theoretical research incorporated protein production and degradation into their model, instead of assuming mass conservation [Tostevin et al., Biophys. J., 2008]. More definitive experimental data on the spatiotemporal changes in protein mass are essential for constructing a more accurate model.

Given the absence of a universally accepted model in agreement with experimental observation, we adopted the assumption that the concentration of molecules in the cytosol (not the total mass on the cell membrane and in the cell cytosol) is spatially inhomogeneous and temporally constant, which was also used before [Kravtsova et al., Bull. Math. Biol., 2014]. In the context of this well-mixed constant cytoplasmic concentration, our model successfully reproduced the cell polarization phenotype in wild-type and eight perturbed conditions (Section 2.5; Fig. S7; Fig. S8), supporting the validity of this simplified, yet effective, model. Now we have provided a discussion of protein mass assumption to foster a more comprehensive understanding in the future.

(18) Comparison of Network Structures: In Figure 1c, the authors demonstrate that the symmetric two-node network is susceptible to single-sided additional regulation. They considered four subtypes of modifications, depending on whether [L] is in the anterior or posterior and whether [A] and [L] are mutually activating or inhibiting. What is the difference between the structure where [L] is in the anterior and in the posterior? Upon comparing the time evolution of the left panel ([L] is sided with

) and the right panel ([L] is sided with [A]), the difference is so tiny that they are almost indistinguishable. It might be beneficial for the authors to provide a clearer explanation of the differences between these network structures to aid in understanding their implications.

We sincerely thank the editor(s) and referee(s) for the constructive suggestion!

The difference between the structures where [L] is in the anterior and posterior is the initial spatial concentration distribution of [L], which is polarized to have a higher concentration in the anterior and posterior respectively. The time evolution of the left panel ([L] is sided with [P]) and the right panel [L] is sided with [P]) is almost indistinguishable because the perturbation from [L] is slight (less than over one order of magnitude) compared to the predominant [A]~[P] interaction ( for [A]~[P] mutual inhibition while for [A]~[L] mutual inhibition and for [A]~[L] mutual activation), highlighting the response of cell polarization pattern. To aid the readers in understanding their implications, we have added the [L] and plotted the spatial concentration distribution of all three molecular species at t=0,100, 200, 300, 400 and 500 in Fig. S3, where the difference between the [L] ones in the left and right panels are distinguishably shown.

(19) Figure Reference: In line 308, Fig. 4a is referenced when explaining the loss of pattern stability by modifying an individual parameter, but this is not shown in that panel. Please update the panel or adjust the reference in the main text.

We sincerely thank the editor(s) and referee(s) for pointing out this problem!

Fig. 4 focuses on the regulatable shift of the zero-velocity interface by modifying a pair of individual parameters, not on the loss (or recovery) of pattern stability, which has been analyzed as a focus in Fig. 1, Fig. 2, and Fig. 3. Fig. 4a is actually from the same simulation as the one in Fig. 1a, which has spatially uniform parameters used as a reference in Fig. 4. The individual parameter modification in other subfigures of Fig. 4 shows how the zero-velocity interface is shifted in a regulatable manner always in the context of pattern stability. Now we update the panel, adjust the reference, add one more paragraph, and improve the wording to clarify how the analyses in Fig. 4 are carried out on top of the pattern stability already studied.

(20) Viable Parameter Sets: In line 355, the number of viable parameter sets (602) is not very informative by itself. We suggest reporting the fraction or percentage of sets tested that resulted in viable results instead. This applies similarly to lines 411 and 468.

We sincerely thank the editor(s) and referee(s) for the constructive comment!

Now the fraction/percentage of parameter sets tested that resulted in viable results are added everywhere the number appears.

(21) Perturbation Experiments: In lines 358-359, "the perturbation experiments" implies that those considered are the only possible ones. Please rephrase to clarify.

We sincerely thank the editor(s) and referee(s) for the helpful advice!

Now we rephrase three paragraphs to clarify why the perturbation experiments involved with [L] and [C] are considered instead of other possible ones.

(22) Figure 2S: This figure is unclear. The caption states that panel (a) shows the "final concentration distribution," but only a line is shown. If "distribution" refers to spatial distribution, please clarify which parameters are shown.

We sincerely thank the editor(s) and referee(s) for pointing out this problem!

Now we clarify the “spatial concentration distribution” and which parameters are shown in the figure caption.

(23) Figure 5 and 6 Captions: The captions for Figures 5 and 6 could benefit from clarification for better understanding.

We sincerely thank the editor(s) and referee(s) for the constructive suggestion!

Now we clarify the details in the captions of Fig. 5 and Fig. 6 for better understanding.

(24) Figure 5 Legend: The legend on the bottom right corner of Figure 5 is unclear. Please specify to which panel it refers.

We sincerely thank the editor(s) and referee(s) for the constructive suggestion!

Now we clarify to which the legend on the bottom right corner of Fig. 5 refers.

(25) L and A~C Interactions: In paragraphs 405-418, please explain why the L and A~C interactions are removed for the comparison instead of others.

We sincerely thank the editor(s) and referee(s) for the constructive suggestion!

Now we add a separate paragraph and a supplemental figure to explain why the L and A~C interactions are removed for the comparison instead of others.

(26) Network Structures in Figure S3: From the "34 possible network structures" considered in Figure S3 (lines 440-441), why are the "null cases" (L disconnected from the network) relevant? Shouldn't only 32 networks be considered?

We sincerely thank the editor(s) and referee(s) for pointing out this problem!

Now the two “null cases” are removed:

(27) Figure S3 Caption: The caption must state that the position of the nodes (left or right) implies the polarisation pattern. Additionally, with the current size of the figure, the dashed lines are extremely hard to differentiate from the continuous lines.

We sincerely thank the editor(s) and referee(s) for the constructive suggestion!

Now we state that the position of the nodes (left or right) implies the polarization pattern. Additionally, we have modified the figure size and dashed lines so that the dash lines are adequately distinguishable from the continuous lines.

(28) Equation #7: It is confusing to use P as the number of independent simulations when P is also one of the variables/species in the network. Please consider using different notation.

We sincerely thank the editor(s) and refer(s) for the hhelpful advice!

Now we replace the P in current Equation #8 with Q and the P in current Equation #10 with W.

(29) Use of "Detailed Balance": The authors used the term "detailed balance" to describe the intricate balance between the two groups of proteins when forming a polarised pattern. However, "detailed balance" is a term with a specific meaning in thermodynamics. Breaking detailed balance is a feature of nonequilibrium systems, and the polarisation phenomenon is evidently a nonequilibrium process. Using the term "detailed balance" may cause confusion, especially for readers with a physics background. It might be advisable to reconsider the terminology to avoid potential confusion and ensure clarity for readers.

We sincerely thank the editor(s) and referee(s) for the constructive suggestion!

To avoid potential confusion and ensure clarity for readers, now we replace “detailed balance” with “balance”, “required balance”, or “interplay” regarding different contexts.

(30) Terminology: The word "molecule" is used where "molecular species" would be more appropriate, e.g., lines 456 and 551. Please revise these instances.

We sincerely thank the editor(s) and referee(s) for the constructive suggestion!

Now we replace all the “molecule” by “molecular species” as suggested.

(31) Section 2.5: This section is confusing. It isn't clear where the "method outlined" (line 464) is nor what "span an iso-velocity surface at vanishing speed" means in line 470. The sentence in lines 486-488, "An expression similar to Eq. 8 enables quantitative prediction...", is too vague. Please clarify these points and specify what the "similar expression" is and where it can be found.

We sincerely thank the editor(s) and referee(s) for the constructive suggestion!

Now we clarify these points and specify the terms as suggested.

(32) Software Mention: The software is only mentioned in the abstract and conclusions. It should also be mentioned where the computational pipeline is described, and the instructions available in the supplementary information need to be referenced in the main text.

We sincerely thank the editor(s) and referee(s) for pointing out this problem!

Now we mention the software where the computational pipeline is described and reference the instructions available in the Supplemental Text.

(33) Supplementary Material References: Several parts of the supplementary material are never referenced in the main text, including Figure S1, Movies S3-S4, and the Instructions for PolarSim. Please reference these in the main text to clarify their relevance and how they fit with the manuscript's narrative.

We sincerely thank the editor(s) and referee(s) for pointing out this problem!

Now we add all the missing references for supplementary materials to the main text properly.

Author response:

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

Preliminary note from the Reviewing Editor:

The evaluations of the two Reviewers are provided for your information. As you can see, their opinions are very different.

Reviewer #1 is very harsh in his/her evaluation. Clearly, we don't expect you to be able to affect one type of actin network without affecting the other, but rather to change the balance between the two. However, he/she also raises some valid points, in particular that more rationale should be added for the perturbations (also mentioned by Reviewer #2). Both Reviewers have also excellent suggestions for improving the presentation of the data.

We sincerely appreciate your and the reviewers’ suggestions. The comments are amended accordingly.

On another point, I was surprised when reading your manuscript that a molecular description of chirality change in cells is presented as a completely new one. Alexander Bershadsky's group has identified several factors (including alpha-actinin) as important regulators of the direction of chirality. The articles are cited, but these important results are not specifically mentioned. Highlighting them would not call into question the importance of your work, but might even provide additional arguments for your model.

We appreciate the editor’s comment. Alexander Bershadsky's group has done marvelous work in cell chirality. They introduced the stair-stepping and screw theory, which suggested how radial fiber polymerization generates ACW force and drives the actin cytoskeleton into the ACW pattern. Moreover, they have identified chiral regulators like alpha-actinin 1, mDia1, capZB, and profilin 1, which can reverse or neutralize the chiral expression.

It is worth noting that Bershadsky's group primarily focuses on radial fibers. In our manuscript, instead, we primarily focused on the contractile unit in the transverse arcs and CW chirality in our investigation. Our manuscript incorporates our findings in the transverse arcs and the radial fibers theory by Bershadsky's group into the chirality balance hypothesis, providing a more comprehensive understanding of the chirality expression.

We have included relevant articles from Alexander Bershadsky's group, we agree that highlighting these important results of chiral regulators would further strengthen our manuscript. The manuscript was revised as follows:

“ACW chirality can be explained by the right-handed axial spinning of radial fibers during polymerization, i.e. ‘stair-stepping' mode proposed by Tee et al. (Tee et al. 2015) (Figure 8A; Video 4). As actin filament is formed in a right-handed double helix, it possesses an intrinsic chiral nature. During the polymerization of radial fiber, the barbed end capped by formin at focal adhesion was found to recruit new actin monomers to the filament. The tethering by formin during the recruitment of actin monomers contributes to the right-handed tilting of radial fibers, leading to ACW rotation. Supporting this model, Jalal et al. (Jalal et al. 2019) showed that the silencing of mDia1, capZB, and profilin 1 would abolish the ACW chiral expression or reverse the chirality into CW direction. Specifically, the silencing of mDia1, capZB or profilin-1 would attenuate the recruitment of actin monomer into the radial fiber, with mDia1 acting as the nucleator of actin filament (Tsuji et al. 2002), CapZB promoting actin polymerization as capping protein (Mukherjee et al. 2016), and profilin-1 facilitating ATP-bound G-actin to the barbed ends(Haarer and Brown 1990; Witke 2004). The silencing resulted in a decrease in the elongation velocity of radial fiber, driving the cell into neutral or CW chirality. These results support that our findings that reduction of radial fiber elongation can invert the balance of chirality expression, changing the ACW-expressing cell into a neutral or CW-expressing cell.”

By incorporating their findings into our revision and discussion, we provide additional support for our radial fiber-transverse arc balance model for chirality expression. The revision is made on pages 8 to 9, 13, lines 253 to 256, 284, 312 to 313, 443, 449 to 459.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Kwong et al. present evidence that two actin-filament based cytoskeletal structures regulate the clockwise and anticlockwise rotation of the cytoplasm. These claims are based on experiments using cells plated on micropatterned substrates (circles). Previous reports have shown that the actomyosin network that forms on the dorsal surface of a cell plated on a circle drives a rotational or swirling pattern of movement in the cytoplasm. This actin network is composed of a combination of non-contractile radial stress fibers (AKA dorsal stress fibers) which are mechanically coupled to contractile transverse actin arcs (AKA actin arcs). The authors claim that directionality of the rotation of the cytoplasm (i.e., clockwise or anticlockwise) depends on either the actin arcs or radial fibers, respectively. While this would interesting, the authors are not able to remove either actin-based network without effecting the other. This is not surprising, as it is likely that the radial fibers require the arcs to elongate them, and the arcs require the radial fibers to stop them from collapsing. As such, it is difficult to make simple interpretations such as the clockwise bias is driven by the arcs and anticlockwise bias is driven by the radial fibers.

Weaknesses:

(1) There are also multiple problems with how the data is displayed and interpreted. First, it is difficult to compare the experimental data with the controls as the authors do not include control images in several of the figures. For example, Figure 6 has images showing myosin IIA distribution, but Figure 5 has the control image. Each figure needs to show controls. Otherwise, it will be difficult for the reader to understand the differences in localization of the proteins shown. This could be accomplished by either adding different control examples or by combining figures.

We appreciate the reviewer’s comment. We agree with the reviewer that it is difficult to compare our results in the current arrangement. The controls are included in the new Figure 6.

(2) It is important that the authors should label the range of gray values of the heat maps shown. It is difficult to know how these maps were created. I could not find a description in the methods, nor have previous papers laid out a standardized way of doing it. As such, the reader needs some indication as to whether the maps showing different cells were created the same and show the same range of gray levels. In general, heat maps showing the same protein should have identical gray levels. The authors already show color bars next to the heat maps indicating the range of colors used. It should be a simple fix to label the minimum (blue on the color bar) and the maximum (red on the color bar) gray levels on these color bars. The profiles of actin shown in Figure 3 and Figure 3- figure supplement 3 were useful for interpretating the distribution of actin filaments. Why did not the authors show the same for the myosin IIa distributions?

We appreciate the reviewer’s comment. For generating the distribution heatmap, the images were taken under the same setting (e.g., fluorescent staining procedure, excitation intensity, or exposure time). The prerequisite of cells for image stacking was that they had to be fully spread on either 2500 µm2 or 750 µm2 circular patterns. Then, the location for image stacking was determined by identifying the center of each cell spread in a perfect circle. Finally, the images were aligned at the cell center to calculate the averaged intensity to show the distribution heatmap on the circular pattern. Revision is made on pages 19 to 20, lines 668 to 677.

It is important to note that the individual heatmaps represent the normalized distribution generated using unique color intensity ranges. This approach was chosen to emphasize the proportional distribution of protein within cells and its variations among samples, especially for samples with generally lower expression levels. Additionally, a differential heatmap with its own range was employed to demonstrate the normalized differences compared to the control sample. Furthermore, to provide additional insight, we plotted the intensity profile of the same protein with the same size for comparative analysis. Revision is made on pages 20, lines 679 to 682.

The labels of the heatmap are included to show the intensity in the revised Figure 3, Figure 5, Figure 6, and Figure 3 —figure supplement 4.

To better illustrate the myosin IIa distribution, the myosin intensity profiles were plotted for Y27 treatment and gene silencing. The figures are included as Figure 5—figure supplement 2 and Figure 6—figure supplement 2. Revisions are made on pages 10, lines 332 to 334 and pages 11, lines 377 to 379.

(3) Line 189 "This absence of radial fibers is unexpected". The authors should clarify what they mean by this statement. The claim that the cell in Figure 3B has reduced radial stress fiber is not supported by the data shown. Every actin structure in this cell is reduced compared to the cell on the larger micropattern in Figure 3A. It is unclear if the radial stress fibers are reduced more than the arcs. Are the authors referring to radial fiber elongation?

We appreciate the reviewer’s comment. We calculated the structures' pixel number and the percentage in the image to better illustrate the reduction of radial fiber or transverse arc. As radial fibers emerge from the cell boundary and point towards the cell center and the transverse arcs are parallel to the cell edge, the actin filament can be identified by their angle with respect to the cell center. We found that the pixel number of radial fiber is greatly reduced by 91.98 % on 750 µm2 compared to the 2500 µm2 pattern, while the pixel number of transverse arc is reduced by 70.58 % (Figure 3- figure supplement 3A). Additionally, we compared the percentage of actin structures on different pattern sizes (Figure 3- figure supplement 3B). On 2500 µm2 pattern, the percentage of radial fiber in the actin structure is 61.76 ± 2.77 %, but it only accounts for 31.13 ± 2.76 % while on 750 µm2 pattern. These results provide evidence of the structural reduction on a smaller pattern.

Regarding the radial fiber elongation, we only discussed the reduction of radial fiber on 750 µm2 compared to the 2500 µm2 pattern in this part. For more understanding of the radial fiber contribution to chirality, we compared the radial fiber elongation rate in the LatA treatment and control on 2500 µm2 pattern (Figure 4). This result suggests the potential role of radial fiber in cell chirality. Revisions are made on page 6, lines 186 to 194; pages 17 to 18, 601 to 606; and the new Figure 3- figure supplement 3.

(4) The choice of the small molecule inhibitors used in this study is difficult to understand, and their results are also confusing. For example, sequestering G actin with Latrunculin A is a complicated experiment. The authors use a relatively low concentration (50 nM) and show that actin filament-based structures are reduced and there are more in the center of the cell than in controls (Figure 3E). What was the logic of choosing this concentration?

We appreciate the reviewer’s comment. The concentration of drugs was selected based on literatures and their known effects on actin arrangement or chiral expression.

For example, Latrunculin A was used at 50 nM concentration, which has been proven effective in reversing the chirality at or below 50 nM (Bao et al., 2020; Chin et al., 2018; Kwong et al., 2019; Wan et al., 2011). Similarly, the 2 µM A23187 treatment concentration was selected to initiate the actin remodeling (Shao et al., 2015). Furthermore, NSC23677 at 100 µM was found to efficiently inhibit the Rac1 activation and resulted in a distinct change in actin structure (Chen et al., 2011; Gao et al., 2004), enhancing ACW chiral expression. The revision is made on pages 6 to 7, lines 202 to 211.

(5) Using a small molecule that binds the barbed end (e.g., cytochalasin) could conceivably be used to selectively remove longer actin filaments, which the radial fibers have compared to the lamellipodia and the transverse arcs. The authors should articulate how the actin cytoskeleton is being changed by latruculin treatment and the impact on chirality. Is it just that the radial stress fibers are not elongating? There seems to be more radial stress fibers than in controls, rather than an absence of radial stress fibers.

We appreciate the reviewer’s comment. Our results showed Latrunculin A treatment reversed the cell chirality. To compare the amount of radial fiber and transverse arc, we calculated the structures' pixel percentage. We found that, the percentage of radial fibers pixel with LatA treatment was reduced compared to that of the control, while the percentage of transverse arcs pixel increased (Figure 3— figure supplement 5). This result suggests that radial fibers are inhibited under Latrunculin A treatment.

Furthermore, the elongation rate of radial fibers is reduced by Latrunculin A treatment (Figure 4). This result, along with the reduction of radial fiber percentage under Latrunculin A treatment suggests the significant impact of radial fiber on the ACW chirality.  Revisions are made on pages 7 to 8, lines 244 to 250 and the new Figure 3— figure supplement 5 and Figure 3— figure supplement 6.

(6) Similar problems arise from the other small molecules as well. LPA has more effects than simply activating RhoA. Additionally, many of the quantifiable effects of LPA treatment are apparent only after the cells are serum starved, which does not seem to be the case here.

We appreciate the reviewer’s comment. The reviewer mentioned that the quantifiable effects of LPA treatments were seen after the cells were serum-starved. LPA is known to be a serum component and has an affinity to albumin in serum (Moolenaar, 1995). Serum starvation is often employed to better observe the effects of LPA by comparing conditions with and without LPA. We agree with the reviewer that the effect of LPA cannot be fully seen under the current setting. Based on the reviewer’s comment and after careful consideration, we have decided to remove the data related to LPA from our manuscript. Revisions are made on pages 6 to 7, 17 and Figure 3— figure supplement 4.

(7) Furthermore, inhibiting ROCK with, Y-27632, effects myosin light chain phosphorylation and is not specific to myosin IIA. Are the two other myosin II paralogs expressed in these cells (myosin IIB and myosin IIC)? If so, the authors’ statements about this experiment should refer to myosin II not myosin IIa.

We appreciate the reviewer’s comment. We agree that ensuring accuracy and clarity in our statements is important. The terminology is revised to myosin II regarding the Y27632 experiment for a more concise description. Revision is made on pages 9 to 10 and 29, lines 317 to 341, 845 and 848.  

(8) None of the uses of the small molecules above have supporting data using a different experimental method. For example, backing up the LPA experiment by perturbing RhoA tho.

We appreciate the reviewer’s comment. After careful consideration, we have decided to remove the data related to LPA from our manuscript. Revisions are made on pages 6 to 7, 17 and Figure 3— figure supplement 4.

(9) The use of SMIFH2 as a "formin inhibitor" is also problematic. SMIFH2 also inhibits myosin II contractility, making interpreting its effects on cells difficult to impossible. The authors present data of mDia2 knockdown, which would be a good control for this SMIFH2.

We appreciate the reviewer’s comment. We agree that there is potential interference of SMIFH2 with myosin II contractility, which could introduce confounding factors to the results. Based on your comment and further consideration, we have decided to remove the data related to SMIFH2 from our manuscript. Revisions are made on pages 6 to 7, 10, 17 and Figure 3— figure supplement 4.

(10) However, the authors claim that mDia2 "typically nucleates tropomyosin-decorated actin filaments, which recruit myosin II and anneal endwise with α-actinin- crosslinked actin filaments."

There is no reference to this statement and the authors own data shows that both arcs and radial fibers are reduced by mDia2 knockdown. Overall, the formin data does not support the conclusions the authors report.

We appreciate the reviewer’s comment. We apologize for the lack of citation for this claim. To address this, we have added a reference to support this claim in the revised manuscript (Tojkander et al., 2011). Revision is made on page 10, line 345 to 347.

Regarding the actin structure of mDia2 gene silencing, our results showed that myosin II was disassociated from the actin filament compared to the control. At the same time, there is no considerable differences in the actin structure of radial fibers and transverse arcs between the mDia2 gene silencing and the control.  

(11) The data in Figure 7 does not support the conclusion that myosin IIa is exclusively on top of the cell. There are clear ventral stress fibers in A (actin) that have myosin IIa localization. The authors simply chose to not draw a line over them to create a height profile.

We appreciate the reviewer’s comment. To better illustrate myosin IIa distribution in a cell, we have included a video showing the myosin IIa staining from the base to the top of the cell (Video 7). At the cell base, the intensity of myosin IIa is relatively low at the center. However, when the focal plane elevates, we can clearly see the myosin II localizes near the top of the cell (Figure 7B and Video 7). Revision is made on page 12, lines 421 to 424, and the new Video 7. 

Reviewer #2 (Public Review):

Summary:

Chirality of cells, organs, and organisms can stem from the chiral asymmetry of proteins and polymers at a much smaller lengthscale. The intrinsic chirality of actin filaments (F-actin) is implicated in the chiral arrangement and movement of cellular structures including F-actin-based bundles and the nucleus. It is unknown how opposite chiralities can be observed when the chirality of F-actin is invariant. Kwong, Chen, and co-authors explored this problem by studying chiral cell-scale structures in adherent mammalian cultured cells. They controlled the size of adhesive patches, and examined chirality at different timepoints. They made various molecular perturbations and used several quantitative assays. They showed that forces exerted by antiparallel actomyosin bundles on parallel radial bundles are responsible for the chirality of the actomyosin network at the cell scale.

Strengths:

Whereas previously, most effort has been put into understanding radial bundles, this study makes an important distinction that transverse or circumferential bundles are made of antiparallel actomyosin arrays. A minor point that was nice for the paper to make is that between the co-existing chirality of nuclear rotation and radial bundle tilt, it is the F-actin driving nuclear rotation and not the other way around. The paper is clearly written.

Weaknesses:

The paper could benefit from grammatical editing. Once the following Major and Minor points are addressed, which may not require any further experimentation and does not entail additional conditions, this manuscript would be appropriate for publication in eLife.

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

Major:

(1) The binary classification of cells as exhibiting clockwise or anticlockwise F-actin structures does not capture the instances where there is very little chirality, such as in the mDia2-depleted cells on small patches (Figure 6B). Such reports of cell chirality throughout the cell population need to be reported as the average angle of F-actin structures on a per cell basis as a rose plot or scatter plot of angle. These changes to cell-scoring and data display will be important to discern between conditions where chirality is random (50% CW, 50% ACW) from conditions where chirality is low (radial bundles are radial and transverse arcs are circumferential).

We appreciate the reviewer’s comment. We apologize if we did not convey our analysis method clearly enough. Throughout the manuscript, unless mentioned otherwise, the chirality analysis was based on the chiral nucleus rotation within a period of observation. The only exception is the F-actin structure chirality, in Figure 3—figure supplement 1, which we analyzed the angle of radial fiber of the control cell on 2500 µm2. It was described on pages 5 to 6, lines 169-172, and the method section “Analysis of fiber orientation and actin structure on circular pattern” on page 17.

Based on the feedback, we attempted to use a scatter plot to present the mDia2 overexpression and silencing to show the randomness of the result. However, because scatter plots primarily focus on visualizing the distribution, they become cluttered and visually overwhelming, as shown below.

Author response image 1.

(A) Percentage of ACW nucleus rotational bias on 2500 µm2 with untreated control (reused data from Figure 3D, n = 57), mDia2 silencing (n = 48), and overexpression (n = 25). (B) Probability of ACW/CW rotation on 750 µm2 pattern with untreated control (reused data from Figure 3E, n = 34), mDia2 silencing (n = 53), and overexpressing (n = 22). Mean ± SEM. Two-sample equal variance two-tailed t-test.

Therefore, in our manuscript, the presentation primarily used a column bar chart with statistical analysis, the Student T-test. The column bar chart makes it easier to understand and compare values. In brief, the Student T-test is commonly used to evaluate whether the means between the two groups are significantly different, assuming equal variance. As such, the Student T-test is able to discern the randomness of the chirality.

(2) The authors need to discuss the likely nucleator of F-actin in the radial bundles, since it is apparently not mDia2 in these cells.

We appreciate the reviewer’s comment. In our manuscript, we originally focused on mDia2 and Tpm4 as they are the transverse arc nucleator and the mediator of myosin II motion. However, we agree with the reviewer that discussing the radial fiber nucleator would provide more insight into radial fiber polymerization in ACW chirality and improve the completeness of the story.

Radial fiber polymerizes at the focal adhesion. Serval proteins are involved in actin nucleation or stress fiber formation at the focal adhesion, such as Arp2/3 complex (Serrels et al., 2007), Ena/VASP (Applewhite et al., 2007; Gateva et al., 2014), and formins (Dettenhofer et al., 2008; Sahasrabudhe et al., 2016; Tsuji et al., 2002), etc. Within the formin family, mDia1 is the likely nucleator of F-actin in the radial bundle. The presence of mDia1 facilitates the elongation of actin bundles at focal adhesion (Hotulainen and Lappalainen, 2006). Studies by Jalal, et al (2019) (Jalal et al., 2019) and Tee, et al (2023) (Tee et al., 2023), have demonstrated the silencing of mDia1 abolished the ACW actin expression. Silencing of other nucleation proteins like Arp2/3 complex or Ena/VASP would only reduce the ACW actin expression without abolishing it.

Based on these findings, the attenuation of radial fiber elongation would abolish the ACW chiral expression, providing more support for our model in explaining chirality expression.

This part is incorporated into the Discussion. The revision is made on page 13, lines 443, 449 to 459.

Minor:

(1) In the introduction, additional observations of handedness reversal need to be referenced (line 79), including Schonegg, Hyman, and Wood 2014 and Zaatri, Perry, and Maddox 2021.

We appreciate the reviewer’s comment. The observations of handedness reversal references are cited on page 3, line 78 to 79.

(2) For clarity of logic, the authors should share the rationale for choosing, and results from administering, the collection of compounds as presented in Figure 3 one at a time instead of as a list.

We appreciate the reviewer’s comment. The concentration of drugs was determined based on existing literature and their known outcomes on actin arrangement or chiral expression.

To elucidate, the use of Latrunculin A was based on previous studies, which have demonstrated to reverse the chirality at or below 50 nM (Bao et al., 2020; Chin et al., 2018; Kwong et al., 2019; Wan et al., 2011).  Because inhibiting F-actin assembly can lead to the expression of CW chirality, we hypothesized that the opposite treatment might enhance ACW chirality. Therefore, we chose A23187 treatment with 2 µM concentration as it could initiate the actin remodeling and stress fiber formation (Shao et al., 2015).

Furthermore, in the attempt to replicate the reversal of chirality by inhibiting F-actin assembly through other pathways, we explored NSC23677 at 100 µM, which was found to inhibit the Rac1 activation (Chen et al., 2011; Gao et al., 2004) and reduce cortical F-actin assembly (Head et al., 2003). However, it failed to reverse the chirality but enhanced the ACW chirality of the cell.

We carefully selected the drugs and the applied concentration to investigate various pathways and mechanisms that influence actin arrangement and might affect the chiral expression. We believe that this clarification strengthens the rationale behind our choice of drug. The revision is made on pages 6 to 7, lines 202 to 211.

(3) "Image stacking" isn't a common term to this referee. Its first appearance in the main text (line 183) should be accompanied with a call-out to the Methods section. The authors could consider referring to this approach more directly. Related issue: Image stacking fails to report the prominent enrichment of F-actin at the very cell periphery (see Figure 3 A and F) except for with images of cells on small islands (Figure 3H). Since this data display approach seems to be adding the intensity from all images together, and since cells on circular adhesive patches are relatively radially symmetric, it is unclear how to align cells, but perhaps cells could be aligned based on a slight asymmetry such as the peripheral location with highest F-actin intensity or the apparent location of the centrosome.

We appreciate the reviewer’s comment. We fully acknowledge the uncommon use of “image stacking” and the insufficient description of image stacking under the Method section. First, we have added a call-out to the Methods section at its first appearance (Page 6, Lines 182 to 183). The method of image stacking is as follows. During generating the distribution heatmap, the images were taken under the same setting (e.g., staining procedure, fluorescent intensity, exposure time, etc.). The prerequisite of cells to be included in image stacking was that they had to be fully spread on either 2500 µm2 or 750 µm2 circular patterns. Then, the consistent position for image stacking could be found by identifying the center of each cell spreading in a perfect circle. Finally, the images were aligned at the center to calculate the averaged intensity to show the distribution heatmap on the circular pattern.

We agree with the reviewer that our image alignment and stacking are based on cells that are radially symmetric. As such, the intensity distribution of stacked image is to compare the difference of F-actin along the radial direction. Revision is made on page 19, lines 668 to 682.

(4) The authors need to be consistent with wording about chirality, avoiding "right" and left (e.g. lines 245-6) since if the cell periphery were oriented differently in the cropped view, the tilt would be a different direction side-to-side but the same chirality. This section is confusing since the peripheral radial bundles are quite radial, and the inner ones are pointing from upper left to lower right, pointing (to the right) more downward over time, rather than more right-ward, in the cropped images.

We appreciate the reviewer’s comment. We apologize for the confusion caused by our description of the tilting direction. For consistency in our later description, we mention the “right” or “left” direction of the radial fibers referencing to the elongation of the radial fiber, which then brings the “rightward tilting” toward the ACW rotation of the chiral pattern. To maintain the word “rightward tilting”, we added the description to ensure accurate communication in our writing. We also rearrange the image in the new Figure 4A and Video 2 for better observation. Revision is made on page 8, lines 262 to 263.

(5) Why are the cells Figure 4A dominated by radial (and more-central, tilting fibers, while control cells in 4D show robust circumferential transverse arcs? Have these cells been plated for different amounts of time or is a different optical section shown?

We appreciate the reviewer’s comment. The cells in Figure 4A and Figure 4D are prepared with similar conditions, such as incubation time and optical setting. Actin organization is a dynamic process, and cells can exhibit varied actin arrangements, transitioning between different forms such as circular, radial, chordal, chiral, or linear patterns, as they spread on a circular island (Tee et al., 2015). In Figure 4A, the actin is arranged in a chiral pattern, whereas in Figure 4D, the actin exhibits a radial pattern. These variations reflect the natural dynamics of actin organization within cells during the imaging process.

(6) All single-color images (such as Fig 5 F-actin) need to be black-on-white, since it is far more difficult to see F-actin morphology with red on black.

We appreciate the reviewer’s comment. We have changed all F-actin images (single color) into black and white for better image clarity. Revisions are made in the new Figure 5, Figure 6 and Figure 7.

(7) Figure 5A, especially the F-actin staining, is quite a bit blurrier than other micrographs. These images should be replaced with images of comparable quality to those shown throughout.

We appreciate the reviewer’s comment. We agree that the F-actin staining in Figure 5 is difficult to observe. To improve image clarity, the F-actin staining images are replaced with more zoomed-in image. Revision is made in the new Figure 5.

(8) F-actin does not look unchanged by Y27632 treatment, as the authors state in line 306. This may be partially due to image quality and the ambiguities of communicating with the blue-to-red colormap. Similarly, I don't agree that mDia2 depletion did not change F-actin distribution (line 330) as cells in that condition had a prominent peripheral ring of F-actin missing from cells in other conditions.

We appreciate the reviewer’s comment. We agree with the reviewer’s observation that the F-actin distribution is indeed changed under Y27632 treatment compared to the control in Figure 5A-B. Here, we would like to emphasize that the actin ring persists despite the actin structure being altered under the Y27632 treatment. The actin ring refers to the darker red circle in the distribution heatmap. It presents the condensed actin structure, including radial fibers and transverse arcs. This important structure remains unaffected despite the disruption of myosin II, the key component in radial fiber.

Furthermore, we agree with the reviewer that mDia2 depletion does change F-actin distribution. Similar to the Y27632 treatment, the actin ring persists despite the actin structure being altered under mDia2 gene silencing. Moreover, compared to other treatments, mDia2 depletion has less significant impact on actin distribution. To address these points more comprehensively, we have made revision in Y27632 treatment and mDia2 sections. The revisions of Y27632 and mDia2 are made on pages 10, lines 324-327 and 352-353, respectively.

(9) The colormap shown for intensity coding should be reconsidered, as dark red is harder to see than the yellow that is sub-maximal. Verdis is a colormap ranging from cooler and darker blue, through green, to warmer and lighter yellow as the maximum. Other options likely exist as well.

We appreciate the reviewer’s comment. We carefully considered the reviewer’s concern and explored other color scale choices in the colormap function in Matlab. After evaluating different options, including “Verdis” color scale, we found that “jet” provides a wide range of colors, allowing the effective visual presentation of intensity variation in our data. The use of ‘jet’ allows us to appropriately visualize the actin ring distribution, which represented in red or dark re. While we understand that dark red could be harder to see than the sub-maximal yellow, we believe that “jet” serves our purpose of presenting the intensity information.

(10) For Figure 6, why doesn't average distribution of NMMIIa look like the example with high at periphery, low inside periphery, moderate throughout lamella, low perinuclear, and high central?

We appreciate the reviewer’s comment. We understand that the reviewer’s concern about the average distribution of NMMIIa not appearing as the same as the example. The chosen image is the best representation of the NMMIIa disruption from the transverse arcs after the mDia2 silencing. Additionally, it is important to note that the average distribution result is a stacked image which includes other images. As such, the NMMIIA example and the distribution heatmap might not necessarily appear identical.

(11) In 2015, Tee, Bershadsky and colleagues demonstrated that transverse bundles are dorsal to radial bundles, using correlative light and electron microscopy. While it is important for Kwong and colleagues to show that this is true in their cells, they should reference Tee et al. in the rationale section of text pertaining to Figure 7.

We appreciate the reviewer’s comment. Tee, et al (Tee et al., 2015) demonstrated the transverse fiber is at the same height as the radial fiber based on the correlative light and electron microscopy. Here, using the position of myosin IIa, a transverse arc component, our results show the dorsal positioning of transverse arcs with connection to the extension of radial fibers (Figure 7C), which is consistent with their findings. It is included in our manuscript, page 12, lines 421 to 424, and page 14 lines 477 to 480.

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Author response:

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

eLife assessment

This important study combines fMRI and electrophysiology in sedated and awake rats to show that LFPs strongly explain spatial correlations in resting-state fMRI but only weakly explain temporal variability. They propose that other, electrophysiology-invisible mechanisms contribute to the fMRI signal. The evidence supporting the separation of spatial and temporal correlations is convincing, however, the support of electrophysiological-invisible mechanisms is incomplete, considering alternative potential factors that could account for the differences in spatial and temporal correlation that were observed. This work will be of interest to researchers who study the fundamental mechanisms behind resting-state fMRI.

We appreciate the encouraging comments. We added a section in discussion that thoroughly discussed the potential alternative factors that could account for the differences in spatial and temporal correlation that we observed. 

Public Reviews:

Reviewer #1 (Public Review):

Tu et al investigated how LFPs recorded simultaneously with rsfMRI explain the spatiotemporal patterns of functional connectivity in sedated and awake rats. They find that connectivity maps generated from gamma band LFPs (from either area) explain very well the spatial correlations observed in rsfMRI signals, but that the temporal variance in rsfMRI data is more poorly explained by the same LFP signals. The authors excluded the effects of sedation in this effect by investigating rats in the awake state (a remarkable feat in the MRI scanner), where the findings generally replicate. The authors also performed a series of tests to assess multiple factors (including noise, outliers, and nonlinearity of the data) in their analysis.

This apparent paradox is then explained by a hypothetical model in which LFPs and neurovascular coupling are generated in some sense "in parallel" by different neuron types, some of which drive LFPs and are measured by ePhys, while others (nNOS, etc.) have an important role in neurovascular coupling but are less visible in Ephys data. Hence the discrepancy is explained by the spatial similarity of neural activity but the more "selective" LFPs picked up by Ephys account for the different temporal aspects observed.

This is a deep, outstanding study that harnesses multidisciplinary approaches (fMRI and ephys) for observing brain activity. The results are strongly supported by the comprehensive analyses done by the authors, which ruled out many potential sources for the observed findings. The study's impact is expected to be very large.

Comment: There are very few weaknesses in the work, but I'd point out that the 1second temporal resolution may have masked significant temporal correlations between

LFPs and spontaneous activity, for instance, as shown by Cabral et al Nature Communications 2023, and even in earlier QPP work from the Keilholz Lab. The synchronization of the LFPs may correlate more with one of these modes than the total signal. Perhaps a kind of "dynamic connectivity" analysis on the authors' data could test whether LFPs correlate better with the activity at specific intervals. However, this could purely be discussed and left for future work, in my opinion.

We appreciate this great point. Indeed, it is likely that LFP and rsfMRI signals are more strongly related during some modes/instances than others, and hence correlation across the entire time series may have masked this effect. In addition, we agree that 1-second temporal resolution may obscure some temporal correlations between LFPs and rsfMRI signal. The choice of 1-second temporal resolution was made to be consistent with the TR in our fMRI experiment, considering the slow hemodynamic response. Ultrafast fMRI imaging combined with dynamic connectivity analysis in a future study might enable more detailed examination of BOLD-LFP temporal correlations at higher temporal resolutions. We have added the following paragraph to the revised manuscript:

“Our proposed theoretic model represents just one potential explanation for the apparent discrepancy in temporal and spatial relationships between resting-state electrophysiology and BOLD signals. It is important to acknowledge that there may be other scenarios where a stronger temporal relationship between LFP and BOLD signals could manifest. For instance, recent research suggests that the relationship between LFP and rsfMRI signals may vary across different modes or instances (Cabral et al., 2023), which can be masked by correlations across the entire time series. Moreover, the 1-second temporal resolution employed in our study may obscure certain temporal correlations between LFPs and rsfMRI signals. Future investigations employing ultrafast fMRI imaging coupled with dynamic connectivity analysis could offer a more nuanced exploration of BOLD-LFP temporal correlations at higher temporal resolutions (Bolt et al., 2022; Cabral et al., 2023; Ma and Zhang, 2018; Thompson et al., 2014).”

Reviewer #2 (Public Review):

The authors address a question that is interesting and important to the sub-field of rsfMRI that examines electrophysiological correlates of rsfMRI. That is, while electrophysiology-produced correlation maps often appear similar to correlation maps produced from BOLD alone (as has been shown in many papers) is this actually coming from the same source of variance, or independent but spatially-correlated sources of variance? To address this, the authors recorded LFP signals in 2 areas (M1 and ACC) and compared the maps produced by correlating BOLD with them to maps produced by BOLD-BOLD correlations. They then attempt to remove various sources of variance and see the results.

The basic concept of the research is sound, though primarily of interest to the subset of rsfMRI researchers who use simultaneous electrophysiology. However, there are major problems in the writing, and also a major methodological problem.

Major problems with writing:

Comment 1: There is substantial literature on rats on site-specific LFP recording compared to rsfMRI, and much of it already examined removing part of the LFP and examining rsfMRI, or vice versa. The authors do not cover it and consider their work on signal removal more novel than it is.

We have added more literature studies to the revised manuscript. It is important to note that while there exists a substantial body of literature on site-specific LFP recording coupled with rsfMRI, our paper makes a significant contribution by unveiling the disparity in temporal and spatial relationships between resting-state electrophysiological and fMRI signals. This goes beyond mere reporting of spatial/temporal correlations. Furthermore, our exploration of the impact of removing LFP on rsfMRI spatial patterns constitutes one among several analyses employed to demonstrate that the temporal fluctuations of LFP minimally affect BOLD-derived RSN spatial patterns. We wish to clarify that our intention is not to claim this aspect of our work is more novel than similar analyses conducted in previous studies (we apologize if our original manuscript conveyed that impression). Rather, the novelty lies in the objective of this analysis, which is to elucidate the displarity in temporal and spatial relationships between resting-state electrophysiological and fMRI signals—a crucial issue that has not been thoroughly addressed previously. 

Comment 2: The conclusion of the existence of an "electrophysiology-invisible signal" is far too broad considering the limited scope of this study. There are many factors that can be extracted from LFP that are not used in this study (envelope, phase, infraslow frequencies under 0.1Hz, estimated MUA, etc.) and there are many ways of comparing it to the rsfMRI data that are not done in this study (rank correlation, transformation prior to comparison, clustering prior to comparison, etc.). The one non-linear method used, mutual information, is low sensitivity and does not cover every possible nonlinear interaction. Mutual information is also dependent upon the number of bins selected in the data. Previous studies (see 1) have seen similar results where fMRI and LFP were not fully commensurate but did not need to draw such broad conclusions.

First we would like to clarify that the existence of "electrophysiologyinvisible signal" is not necessarily a conclusion of the present study, per se, as described by the reviewer. As we stated in our manuscript, it is a proposed theoretical model. We fully acknowledge that this model represents just one potential explanation for the apparent discrepancy in temporal and spatial relationships between resting-state electrophysiology and BOLD signals. It is important to acknowledge that there may be other scenarios where a stronger temporal relationship between LFP and BOLD signals could manifest. This issue has been further clarified in the revised manuscript (see the section of Potential pitfalls). 

We agree with the reviewer that not all factors that can be extracted from LFP are examined. In our current study we focused solely on band-limited LFP power as the primary feature in our analysis, given its prevalence in prior studies of LFP-rsfMRI correlates. More importantly, we demonstrate that band-specific LFP powers can yield spatial patterns nearly identical to those derived from rsfMRI signals, prompting a closer examination of the temporal relationship between these same features. Furthermore, since correlational analysis was used in studying the LFP-BOLD spatial relationship, we used the same analysis method when comparing their temporal relationship. 

Extracting all possible features from the electrophysiology signal and examining their relationship with the rsfMRI signal or exploring all other types of ways of comparing LFP and rsfMRI signals goes beyond the scope of the current study. However, to address the reviewer’s concern, we tried a couple of analysis methods suggested by the reviewer, and results remain persistent. Figure S14 shows the results from (A) the rank correlation and (B) z transformation prior to comparison. We added these new results to the revised manuscript.

Comment 3: The writing refers to the spatial extent of correlation with the LFP signal as "spatial variance." However, LFP was recorded from a very limited point and the variance in the correlation map does not necessarily reflect underlying electrophysiological spatial distributions (e.g. Yu et al. Nat Commun. 2023 Mar 24;14(1):1651.)

The reviewer accurately pointed out that in our paper, “spatial variance” refers to the spatial variance of BOLD correlates with the LFP signal. Our objective is to assess the extent to which this spatial variance, which is derived from the neural activity captured by LFP in the M1 or ACC, corresponds to the BOLD-derived spatial patterns from the same regions. We acknowledge that this spatial variance may differ from the spatial map obtained by multi-site electrophysiology recordings. Nevertheless, numerous studies have consistently reported a high spatial correspondence between BOLD- and electrophysiology-derived RSNs using various methodologies across different physiological states in both humans and animals. For instance, research employing electroencephalography (EEG) or electrocorticography (ECoG) in humans demonstrates that RSNs derived from the power of multiple-site electrophysiological signals exhibit similar spatial patterns to classic BOLD-derived RSNs such as the default-mode network (Hacker et al., 2017; Kucyi et al., 2018). These studies well agree with our findings. Notably, the reference paper cited by the reviewer studies brain-wide changes during transitions between awake and various sleep stages, which is quite different from the brain states examined in our study.

Major method problem:

Comment 4: Correlating LFP to fMRI is correlating two biological signals, with unknown but presumably not uniform distributions. However, correlating CC results from correlation maps is comparing uniform distributions. This is not a fair comparison, especially considering that the noise added is also uniform as it was created with the rand() function in MATLAB.

This is a good point. We examined the distributions of both LFP powers and fMRI signals. They both seem to follow a normal distribution. Below shows distributions of the two signals from a random scan. In addition, z transformation prior to comparison generated the same results (Fig. S14).

Author response image 1.

Exemplar distributions of A) the fMRI signal of M1, and B) HRF-convolved LFP power in M1.

Reviewer #1 (Recommendations For The Authors):

Comment 1: In the Discussion, a few more calcium imaging papers could be fruitfully discussed (e.g. Ma et al Resting-state hemodynamics are spatiotemporally coupled to synchronized and symmetric neural activity in excitatory neurons, PNAS 2016, or more recently Vafaii et al, Multimodal measures of spontaneous brain activity reveal both common and divergent patterns of cortical functional organization, Nat Comms 2024).

We appreciate this suggestion. We have added the following discussions to the revised manuscript: 

“These findings indicate the temporal information provided by gamma power can only explain a minor portion (approximately 35%) of the temporal variance in the BOLD time series, even after accounting for the noise effect, which is in line with the reported correlation value between the cerebral blood volume and fluctuations in GCaMP signal in head-fixed mice during periods of immobility (R = 0.63) (Ma et al., 2016).” 

“It is plausible that employing different features or comparison methods could yield a stronger BOLD-electrophysiology temporal relationship (Ma et al., 2016).”

“Furthermore, in a more recent study by Vafaii and colleagues, overlapping cortical networks were identified using both fMRI and calcium imaging modalities, suggesting that networks observable in fMRI studies exhibit corresponding neural activity spatial patterns (Vafaii et al., 2024).” 

“Furthermore, Vafaii et. al. revealed notable differences in functional connectivity strength measured by fMRI and calcium imaging, despite an overlapping spatial pattern of cortical networks identified by both modalities (Vafaii et al., 2024).”

Comment 2: Similarly when discussing the "invisible" populations, perhaps Uhlirova et al eLife 2016 should be mentioned as some types of inhibitory processes may also be less clearly observed in LFPs but rather strongly contribute to NVC.

We appreciate the suggestion. We added the following sentences to the revised manuscript. 

“Additionally, Uhlirova et al. conducted a study where they utilized optogenetic stimulation and two-photon imaging to investigate how the activation of different neuron types affects blood vessels in mice. They discovered that only the activation of inhibitory neurons led to vessel constriction, albeit with a negligible impact on LFP (Uhlirova et al., 2016).”

Reviewer #2 (Recommendations For The Authors):

Major problems with writing:

Comment 1: The authors need to review past work to better place their study in the context of the literature (some review articles: Lurie et al. Netw Neurosci. 2020 Feb 1;4(1):30-69. & Thompson et al. Neuroimage. 2018 Oct 15;180(Pt B):448-462.)

Here are some LFP and BOLD "resting state" papers focused on dynamic changes.

Many of these papers examine both spatial and temporal extents of correlations. Several of these papers use similar methods to the reviewed paper.

Also, many of these papers dispute the claim that correlations seen are

"electrophysiology invisible signal." Note that I am NOT saying that "electrophysiology invisible" correlations do not exist (it seems very likely some DO exist). However, the authors did not show that in the reviewed paper, and some of the correlations which they call an "electrophysiology invisible signal" probably would be visible if analyzed in a different manner.

Quite a few literature studies that the reviewer suggested were already included in the original manuscript. We have also added more literature studies to the revised manuscript. Again, we would like to emphasize that the novelty of our study centers on the discovery of the disparity in temporal and spatial relationships between resting-state electrophysiological and fMRI signals. See below our responses to individual literature studies listed.

In humans:

https://pubmed.ncbi.nlm.nih.gov/38082179/ Predicts by using models the paper under review does not use here.

The following discussion was added to the revised manuscript: 

“Some other comparison methods such as rank correlation and transformation prior to comparison were also tested and results remain persistent (Fig. S14). These findings align with the notion that, compared to nonlinear models, linear models offer superior predictive value for the rsfMRI signal using LFP data, as comprehensively illustrated in (Nozari et al., 2024) (also see Fig. S7). Importantly, in this study, the predictive powers (represented by R2) of various comparison methods tested all remain below 0.5 (Nozari et al., 2024), suggesting that while certain models may enhance the temporal relationship between LFP and BOLD signals, the improvement is likely modest.”

In nonhuman primates: https://pubmed.ncbi.nlm.nih.gov/34923136/ Most of the variance that could be creating resting state networks is in the <1 Hz band which the paper under review did not study

]We also examined infraslow LFP activity (< 1Hz) in our data. Consistent with the finding in the reference paper (Li et al., 2022), infraslow LFP power and the BOLD signal can derive consistent RSN spatial patterns (for M1, spatial correlation = 0.70), while the temporal correlation remains very low (temporal correlation = 0.08). These results and the reference paper were added to the revised manuscript.

https://pubmed.ncbi.nlm.nih.gov/28461461/ Compares actual spread of LFP vs. spread of BOLD instead of just correlation between LFP and BOLD.

The following sentence has been added to the revised manuscript.

“This high spatial correspondence between rsfMRI and LFP signals can even be found at the columnar level (Shi et al., 2017).”   

https://pubmed.ncbi.nlm.nih.gov/24048850/ Comparison of small (from LFP) to large (from BOLD) spatial correlations in the context of temporal correlations.

In this study, researchers compared neurophysiological maps and fMRI maps of the inferior temporal cortex in macaques in response to visual images. They observed that the spatial correlation increased as the neurophysiological maps got greater levels of spatial smoothing. This suggests that fMRI can capture large-scale spatial information, but it may be limited in capturing fine details. Although interesting, this paper did not study the electrophysiology-fMRI relationship at the resting state and hence is not very relevant to our study.

https://pubmed.ncbi.nlm.nih.gov/20439733/ Electrophysiology from a single site can correlate across nearly the entire cerebral cortex.

We have included the discussion of this paper in the original manuscript.

https://pubmed.ncbi.nlm.nih.gov/18465799/ The original dynamic BOLD and LFP work from 2008 by Shmuel and Leopold included spatiotemporal dynamics.

We have included the discussion of this paper in the original manuscript.

In rodents:

https://pubmed.ncbi.nlm.nih.gov/34296178/ Better electrophysiological correspondence was found using alternate methods the paper under review does not use.

This study investigates the electrophysiological correspondence in taskbased fMRI, while our study focused on resting state signals.

https://pubmed.ncbi.nlm.nih.gov/31785420/ Electrophysiological basis of co-activation patterns, similar comparisons to the paper under review.

We have included the discussion of this paper in the original manuscript.

https://pubmed.ncbi.nlm.nih.gov/29161352/ Cross-frequency coupling of LFP modulating the BOLD, perhaps more so than raw amplitudes.

This paper investigated the impact of AMPA microinjections in the VTA and found reduced ventral striatal functional connectivity, correlation between the delta band and BOLD signal, and phase–amplitude coupling of low-frequency LFP and highfrequency LFP, suggesting changes in low-frequency LFP might modulate the BOLD signal.

Consistent with our study, we also found that low-frequency LFP is negatively coupled with the BOLD signal, but we did not investigate changes in neurovascular coupling with disturbed neural activity using pharmacological methods, and hence, we did not discuss this paper in our study.

https://pubmed.ncbi.nlm.nih.gov/24071524/ This paper did the same kind of tests comparing LFP-BOLD correlations to BOLD-BOLD correlations as the paper under review.

This study examined the neural mechanism underpinning dynamic restingstate fMRI, revealing a spatiotemporal coupling of infra-slow neural activity with a quasiperiodic pattern (QPP). While our current investigation centered on stationary restingstate functional connectivity, we acknowledge that dynamic analysis will provide additional value for investigating the relationship between LFP and rsfMRI signals. This warrants more investigation in a future study. This point has been added to the revised manuscript.

https://pubmed.ncbi.nlm.nih.gov/24904325/ This paper found that different frequencies of electrophysiology (including ones not studied in the reviewed paper) contribute independently to the BOLD signal

This paper identified phase-amplitude coupling in rats anesthetized with isoflurane but not with dexmedetomidine, indicating that this coupling arises from a special type of neural activity pattern, burst-suppression, which was probably induced by high-dose isoflurane. They conjectured that high and low-frequency neural activities may independently or differentially influence the BOLD signal. Our study also examined the influence of various LFP frequency bands on the BOLD signal and found inversed LFP-BOLD relationship between low- and high-frequency LFP powers. We also added more results on the analysis of infraslow LFP signals. Regardless, since the reference study did not examine the spatial relationship of LFP and BOLD activities, we cannot comment on how it may provide insight into our results. 

https://pubmed.ncbi.nlm.nih.gov/26041826/ This paper found electrophysiological correlates within the BOLD signal when using BOLD analysis methods not used in the reviewed paper, and furthermore that some of these correlate with electrophysiological frequencies not studied in the reviewed paper (< 1 Hz).

We have added more results on the analysis of infraslow LFP signals and acknowledged the value of dynamic rsfMRI analysis in studies of BOLDelectrophysiology relationship.

I am not saying the authors need to use all these methods or even cite these papers. As I stated in their review, they merely need to (1) cite some of the most relevant for the proper context, the above list can maybe help (2) remove the claim of an "electrophysiology invisible signal" (3) use terms more commonly used in these papers for the extent of correlation with the electrode, other than "spatial variance."

We thank the reviewer again for providing a detailed list of reference studies. We have added the related discussion to the revised manuscript as described above.

Comment 2: The abstract entirely and much of the rest of the paper should be rewritten to be more reasonable. The authors would do well to review some of the past controversies in this area, e.g. Magri et al. J Neurosci. 2012 Jan 25;32(4):1395-407.

We have made significant revision to improve the writing of the paper. The reference paper has been added to the revised manuscript.

Comment 3: This should be re-written and the terminology used here should be chosen more carefully.

The writing of the manuscript has been improved with more careful choice of terminology.    

Major method problem:

Comment 4: At a minimum, the authors should be transforming the uniform distribution of CC results to Z or T values and using randn() instead of rand() in MATLAB.

Below is the figure illustrating the simulation results by transforming CC values to Z score. Results obtained remain consistent.

Author response image 2.

Minor problems:

Comment 5: "MR-510 compatible electrodes (MRCM16LP, NeuroNexus Inc)"

Details of this type of electrode are not readily available. But for studies like this one, further information on materials is critical as this determines the frequency coverage, which is not even across all LFP frequencies for all materials. Most commercially prepared electrodes cannot record <1Hz accurately, and this study includes at least 0.11Hz in some of its analysis.

The type of electrode used in our current study is a silicon-based micromachined probe. These probes are fabricated using photolithographic techniques to pattern thin layers of conductive materials onto a silicon substrate. This probe is capable of recording the LFP activity within a broad frequency range, starting from 0.1Hz . We added this information to the revised manuscript. 

Comment 6: Grounding to the cerebellum in theory would remove global conduction from the LFP but also global signal regression is done to the fMRI. Does the LFP-rsfMRI correlation change due to the regression or does only the rsfMRI-rsfMRI correlation change?

The results obtained with global signal regression were consistent with those obtained without it (see Figs. S4-S5), and therefore, we do not believe our results are affected by this preprocessing step. 

Comment 7. Avoid colloquial language like "on the other hand" etc.

We used more appropriate language in the revised manuscript.

References:

Bolt, T., Nomi, J.S., Bzdok, D., Salas, J.A., Chang, C., Thomas Yeo, B.T., Uddin, L.Q., Keilholz, S.D., 2022. A parsimonious description of global functional brain organization in three spatiotemporal patterns. Nat Neurosci 25, 1093-1103.

Cabral, J., Fernandes, F.F., Shemesh, N., 2023. Intrinsic macroscale oscillatory modes driving long range functional connectivity in female rat brains detected by ultrafast fMRI. Nat Commun 14, 375.

Hacker, C.D., Snyder, A.Z., Pahwa, M., Corbetta, M., Leuthardt, E.C., 2017. Frequencyspecific electrophysiologic correlates of resting state fMRI networks. Neuroimage 149, 446-457.

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Author response:

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

eLife assessment

This important study provides solid evidence that both psychiatric dimensions (e.g. anhedonia, apathy, or depression) and chronotype (i.e., being a morning or evening person) influence effort-based decision-making. Notably, the current study does not elucidate whether there may be interactive effects of chronotype and psychiatric dimensions on decision-making. This work is of importance to researchers and clinicians alike, who may make inferences about behaviour and cognition without taking into account whether the individual may be tested or observed out-of-sync with their phenotype.

We thank the three reviewers for their comments, and the Editors at eLife. We have taken the opportunity to revise our manuscript considerably from its original form, not least because we feel a number of the reviewers’ suggested analyses strengthen our manuscript considerably (in one instance even clarifying our conclusions, leading us to change our title)—for which we are very appreciative indeed. 

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This study uses an online cognitive task to assess how reward and effort are integrated in a motivated decision-making task. In particular the authors were looking to explore how neuropsychiatric symptoms, in particular apathy and anhedonia, and circadian rhythms affect behavior in this task. Amongst many results, they found that choice bias (the degree to which integrated reward and effort affects decisions) is reduced in individuals with greater neuropsychiatric symptoms, and late chronotypes (being an 'evening person').

Strengths:

The authors recruited participants to perform the cognitive task both in and out of sync with their chronotypes, allowing for the important insight that individuals with late chronotypes show a more reduced choice bias when tested in the morning.<br /> Overall, this is a well-designed and controlled online experimental study. The modelling approach is robust, with care being taken to both perform and explain to the readers the various tests used to ensure the models allow the authors to sufficiently test their hypotheses.

Weaknesses:

This study was not designed to test the interactions of neuropsychiatric symptoms and chronotypes on decision making, and thus can only make preliminary suggestions regarding how symptoms, chronotypes and time-of-assessment interact.

We appreciate the Reviewer’s positive view of our research and agree with their assessment of its weaknesses; the study was not designed to assess chronotype-mental health interactions. We hope that our new title and contextualisation makes this clearer. We respond in more detail point-by-point below.

Reviewer #2 (Public Review):

Summary:

The study combines computational modeling of choice behavior with an economic, effort-based decision-making task to assess how willingness to exert physical effort for a reward varies as a function of individual differences in apathy and anhedonia, or depression, as well as chronotype. They find an overall reduction in effort selection that scales with apathy and anhedonia and depression. They also find that later chronotypes are less likely to choose effort than earlier chronotypes and, interestingly, an interaction whereby later chronotypes are especially unwilling to exert effort in the morning versus the evening.

Strengths:

This study uses state-of-the-art tools for model fitting and validation and regression methods which rule out multicollinearity among symptom measures and Bayesian methods which estimate effects and uncertainty about those estimates. The replication of results across two different kinds of samples is another strength. Finally, the study provides new information about the effects not only of chronotype but also chronotype by timepoint interactions which are previously unknown in the subfield of effort-based decision-making.

Weaknesses:

The study has few weaknesses. One potential concern is that the range of models which were tested was narrow, and other models might have been considered. For example, the Authors might have also tried to fit models with an overall inverse temperature parameter to capture decision noise. One reason for doing so is that some variance in the bias parameter might be attributed to noise, which was not modeled here. Another concern is that the manuscripts discuss effort-based choice as a transdiagnostic feature - and there is evidence in other studies that effort deficits are a transdiagnostic feature of multiple disorders. However, because the present study does not investigate multiple diagnostic categories, it doesn't provide evidence for transdiagnosticity, per se.

We appreciate Reviewer 2’s assessment of our research and agree generally with its weaknesses. We have now addressed the Reviewer’s comments regarding transdiagnosticity in the discussion of our revised version and have addressed their detailed recommendations below (see point-by-point responses).

In addition to the below specific changes, in our Discussion section, we now have also added the following (lines 538 – 540):

“Finally, we would like to note that as our study is based on a general population sample, rather than a clinical one. Hence, we cannot speak to transdiagnosticity on the level of multiple diagnostic categories.”

Reviewer #3 (Public Review):

Summary:

In this manuscript, Mehrhof and Nord study a large dataset of participants collected online (n=958 after exclusions) who performed a simple effort-based choice task. They report that the level of effort and reward influence choices in a way that is expected from prior work. They then relate choice preferences to neuropsychiatric syndromes and, in a smaller sample (n<200), to people's circadian preferences, i.e., whether they are a morning-preferring or evening-preferring chronotype. They find relationships between the choice bias (a model parameter capturing the likelihood to accept effort-reward challenges, like an intercept) and anhedonia and apathy, as well as chronotype. People with higher anhedonia and apathy and an evening chronotype are less likely to accept challenges (more negative choice bias). People with an evening chronotype are also more reward sensitive and more likely to accept challenges in the evening, compared to the morning.

Strengths:

This is an interesting and well-written manuscript which replicates some known results and introduces a new consideration related to potential chronotype relationships which have not been explored before. It uses a large sample size and includes analyses related to transdiagnostic as well as diagnostic criteria. I have some suggestions for improvements.

Weaknesses:

(1) The novel findings in this manuscript are those pertaining to transdiagnostic and circadian phenotypes. The authors report two separate but "overlapping" effects: individuals high on anhedonia/apathy are less willing to accept offers in the task, and similarly, individuals tested off their chronotype are less willing to accept offers in the task. The authors claim that the latter has implications for studying the former. In other words, because individuals high on anhedonia/apathy predominantly have a late chronotype (but might be tested early in the day), they might accept less offers, which could spuriously look like a link between anhedonia/apathy and choices but might in fact be an effect of the interaction between chronotype and time-of-testing. The authors therefore argue that chronotype needs to be accounted for when studying links between depression and effort tasks.

The authors argue that, if X is associated with Y and Z is associated with Y, X and Z might confound each other. That is possible, but not necessarily true. It would need to be tested explicitly by having X (anhedonia/apathy) and Z (chronotype) in the same regression model. Does the effect of anhedonia/apathy on choices disappear when accounting for chronotype (and time-of-testing)? Similarly, when adding the interaction between anhedonia/apathy, chronotype, and time-of-testing, within the subsample of people tested off their chronotype, is there a residual effect of anhedonia/apathy on choices or not?

If the effect of anhedonia/apathy disappeared (or got weaker) while accounting for chronotype, this result would suggest that chronotype mediates the effect of anhedonia/apathy on effort choices. However, I am not sure it renders the direct effect of anhedonia/apathy on choices entirely spurious. Late chronotype might be a feature (induced by other symptoms) of depression (such as fatigue and insomnia), and the association between anhedonia/apathy and effort choices might be a true and meaningful one. For example, if the effect of anhedonia/apathy on effort choices was mediated by altered connectivity of the dorsal ACC, we would not say that ACC connectivity renders the link between depression and effort choices "spurious", but we would speak of a mechanism that explains this effect. The authors should discuss in a more nuanced way what a significant mediation by the chronotype/time-of-testing congruency means for interpreting effects of depression in computational psychiatry.

We thank the Reviewer for pointing out this crucial weakness in the original version of our manuscript. We have now thought deeply about this and agree with the Reviewer that our original results did not warrant our interpretation that reported effects of anhedonia and apathy on measures of effort-based decision-making could potentially be spurious. At the Reviewer’s suggestion, we decided to test this explicitly in our revised version—a decision that has now deepened our understanding of our results, and changed our interpretation thereof.  

To investigate how the effects of neuropsychiatric symptoms and the effects of circadian measures relate to each other, we have followed the Reviewer’s advice and conducted an additional series of analyses (see below). Surprisingly (to us, but perhaps not the Reviewer) we discovered that all three symptom measures (two of anhedonia, one of apathy) have separable effects from circadian measures on the decision to expend effort (note we have also re-named our key parameter ‘motivational tendency’ to address this Reviewer’s next comment that the term ‘choice bias’ was unclear). In model comparisons (based on leave-one-out information criterion which penalises for model complexity) the models including both circadian and psychiatric measures always win against the models including either circadian or psychiatric measures. In essence, this strengthens our claims about the importance of measuring circadian rhythm in effort-based tasks generally, as circadian rhythm clearly plays an important role even when considering neuropsychiatric symptoms, but crucially does not support the idea of spurious effects: statistically, circadian measures contributes separably from neuropsychiatric symptoms to the variance in effort-based decision-making. We think this is very interesting indeed, and certainly clarifies (and corrects the inaccuracy in) our original interpretation—and can only express our thanks to the Reviewer for helping us understand our effect more fully.

In response to these new insights, we have made numerous edits to our manuscript. First, we changed the title from “Overlapping effects of neuropsychiatric symptoms and circadian rhythm on effort-based decision-making” to “Both neuropsychiatric symptoms and circadian rhythm alter effort-based decision-making”. In the remaining manuscript we now refrain from using the word ‘overlapping’ (which could be interpreted as overlapping in explained variance), and instead opted to describe the effects as parallel. We hope our new analyses, title, and clarified/improved interpretations together address the Reviewer’s valid concern about our manuscript’s main weakness.

We detail these new analyses in the Methods section as follows (lines 800 – 814):

“4.5.2. Differentiating between the effects of neuropsychiatric symptoms and circadian measures on motivational tendency

To investigate how the effects of neuropsychiatric symptoms on motivational tendency (2.3.1) relate to effects of chronotype and time-of-day on motivational tendency we conducted exploratory analyses. In the subsamples of participants with an early or late chronotype (including additionally collected data), we first ran Bayesian GLMs with neuropsychiatric questionnaire scores (SHAPS, DARS, AES respectively) predicting motivational tendency, controlling for age and gender. We next added an interaction term of chronotype and time-of-day into the GLMs, testing how this changes previously observed neuropsychiatric and circadian effects on motivational tendency. Finally, we conducted a model comparison using LOO, comparing between motivational tendency predicted by a neuropsychiatric questionnaire, motivational tendency predicted by chronotype and time-of-day, and motivational tendency predicted by a neuropsychiatric questionnaire and time-of-day (for each neuropsychiatric questionnaire, and controlling for age and gender).”

Results of the outlined analyses are reported in the results section as follows (lines 356 – 383):

“2.5.2.1 Neuropsychiatric symptoms and circadian measures have separable effects on motivational tendency

Exploratory analyses testing for the effects of neuropsychiatric questionnaires on motivational tendency in the subsamples of early and late chronotypes confirmed the predictive value of the SHAPS (M=-0.24, 95% HDI=[-0.42,-0.06]), the DARS (M=-0.16, 95% HDI=[-0.31,-0.01]), and the AES (M=-0.18, 95% HDI=[-0.32,-0.02]) on motivational tendency.

For the SHAPS, we find that when adding the measures of chronotype and time-of-day back into the GLMs, the main effect of the SHAPS (M=-0.26, 95% HDI=[-0.43,-0.07]), the main effect of chronotype (M=-0.11, 95% HDI=[-0.22,-0.01]), and the interaction effect of chronotype and time-of-day (M=0.20, 95% HDI=[0.07,0.34]) on motivational tendency remain. Model comparison by LOOIC reveals motivational tendency is best predicted by the model including the SHAPS, chronotype and time-of-day as predictors, followed by the model including only the SHAPS. Note that this approach to model comparison penalizes models for increasing complexity.

Repeating these steps with the DARS, the main effect of the DARS is found numerically, but the 95% HDI just includes 0 (M=-0.15, 95% HDI=[-0.30,0.002]). The main effect of chronotype (M=-0.11, 95% HDI=[-0.21,-0.01]), and the interaction effect of chronotype and time-of-day (M=0.18, 95% HDI=[0.05,0.33]) on motivational tendency remain. Model comparison identifies the model including the DARS and circadian measures as the best model, followed by the model including only the DARS.

For the AES, the main effect of the AES is found (M=-0.19, 95% HDI=[-0.35,-0.04]). For the main effect of chronotype, the 95% narrowly includes 0 (M=-0.10, 95% HDI=[-0.21,0.002]), while the interaction effect of chronotype and time-of-day (M=0.20, 95% HDI=[0.07,0.34]) on motivational tendency remains. Model comparison identifies the model including the AES and circadian measures as the best model, followed by the model including only the AES.”

We have now edited parts of our Discussion to discuss and reflect these new insights, including the following.

Lines 399 – 402:

“Various neuropsychiatric disorders are marked by disruptions in circadian rhythm, such as a late chronotype. However, research has rarely investigated how transdiagnostic mechanisms underlying neuropsychiatric conditions may relate to inter-individual differences in circadian rhythm.”

Lines 475 – 480:

“It is striking that the effects of neuropsychiatric symptoms on effort-based decision-making largely are paralleled by circadian effects on the same neurocomputational parameter. Exploratory analyses predicting motivational tendency by neuropsychiatric symptoms and circadian measures simultaneously indicate the effects go beyond recapitulating each other, but rather explain separable parts of the variance in motivational tendency.”

Lines 528 – 532:

“Our reported analyses investigating neuropsychiatric and circadian effects on effort-based decision-making simultaneously are exploratory, as our study design was not ideally set out to examine this. Further work is needed to disentangle separable effects of neuropsychiatric and circadian measures on effort-based decision-making.”

Lines 543 – 550:

“We demonstrate that neuropsychiatric effects on effort-based decision-making are paralleled by effects of circadian rhythm and time-of-day. Exploratory analyses suggest these effects account for separable parts of the variance in effort-based decision-making. It unlikely that effects of neuropsychiatric effects on effort-based decision-making reported here and in previous literature are a spurious result due to multicollinearity with chronotype. Yet, not accounting for chronotype and time of testing, which is the predominant practice in the field, could affect results.”

(2) It seems that all key results relate to the choice bias in the model (as opposed to reward or effort sensitivity). It would therefore be helpful to understand what fundamental process the choice bias is really capturing in this task. This is not discussed, and the direction of effects is not discussed either, but potentially quite important. It seems that the choice bias captures how many effortful reward challenges are accepted overall which maybe captures general motivation or task engagement. Maybe it is then quite expected that this could be linked with questionnaires measuring general motivation/pleasure/task engagement. Formally, the choice bias is the constant term or intercept in the model for p(accept), but the authors never comment on what its sign means. If I'm not mistaken, people with higher anhedonia but also higher apathy are less likely to accept challenges and thus engage in the task (more negative choice bias). I could not find any discussion or even mention of what these results mean. This similarly pertains to the results on chronotype. In general, "choice bias" may not be the most intuitive term and the authors may want to consider renaming it. Also, given the sign of what the choice bias means could be flipped with a simple sign flip in the model equation (i.e., equating to accepting more vs accepting less offers), it would be helpful to show some basic plots to illustrate the identified differences (e.g., plotting the % accepted for people in the upper and lower tertile for the SHAPS score etc).

We apologise that this was not made clear previously: the meaning and directionality of “choice bias” is indeed central to our results. We also thank the Reviewer for pointing out the previousely-used term “choice bias” itself might not be intuitive. We have now changed this to ‘motivational tendency’ (see below) as well as added substantial details on this parameter to the manuscript, including additional explanations and visualisations of the model as suggested by the Reviewer (new Figure 3) and model-agnostic results to aid interpretation (new Figure S3). Note the latter is complex due to our staircasing procedure (see new figure panel D further detailing our staircasing procedure in Figure 2). This shows that participants with more pronounced anhedonia are less likely to accept offers than those with low anhedonia (Fig. S3A), a model-agnostic version of our central result.

Our changes are detailed below:

After careful evaluation we have decided to term the parameter “motivational tendency”, hoping that this will present a more intuitive description of the parameter.

To aid with the understanding and interpretation of the model parameters, and motivational tendency in particular, we have added the following explanation to the main text:

Lines 149 – 155:

“The models posit efforts and rewards are joined into a subjective value (SV), weighed by individual effort (and reward sensitivity (parameters. The subjective value is then integrated with an individual motivational tendency (a) parameter to guide decision-making. Specifically, the motivational tendency parameter determines the range at which subjective values are translated to acceptance probabilities: the same subjective value will translate to a higher acceptance probability the higher the motivational tendency.”

Further, we have included a new figure, visualizing the model. This demonstrates how the different model parameters contribute to the model (A), and how different values on each parameter affects the model (B-D).

We agree that plotting model agnostic effects in our data may help the reader gain intuition of what our task results mean. We hope to address this with our added section on “Model agnostic task measures relating to questionnaires”. We first followed the reviewer’s suggestion of extracting subsamples with higher and low anhedonia (as measured with the SHAPS, highest and lowest quantile) and plotted the acceptance proportion across effort and reward levels (panel A in figure below). However, due to our implemented task design, this only shows part of the picture: the staircasing procedure individualises which effort-reward combination a participant is presented with. Therefore, group differences in choice behaviour will lead to differences in the development of the staircases implemented in our task. Thus, we plotted the count of offered effort-reward combinations for the subsamples of participants with high vs. low SHAPS scores by the end of the task, averaged across staircases and participants.

As the aspect of task development due to the implemented staircasing may not have been explained sufficiently in the main text, we have included panel (D) in figure 2.

Further, we have added the following figure reference to the main text (lines 189 – 193):

“The development of offered effort and reward levels across trials is shown in figure 2D; this shows that as participants generally tend to accept challenges rather than reject them, the implemented staircasing procedure develops toward higher effort and lover reward challenges.”

To statistically test effects of model-agnostic task measures on the neuropsychiatric questionnaires, we performed Bayesian GLMs with the proportion of accepted trials predicted by SHAPS and AES. This is reported in the text as follows.

Supplement, lines 172 – 189:

“To explore the relationship between model agnostic task measures to questionnaire measures of neuropsychiatric symptoms, we conducted Bayesian GLMs, with the proportion of accepted trials predicted by SHAPS scores, controlling for age and gender. The proportion of accepted trials averaged across effort and reward levels was predicted by the Snaith-Hamilton Pleasure Scale (SHAPS) sum scores (M=-0.07; 95%HDI=[-0.12,-0.03]) and the Apathy Evaluation Scale (AES) sum scores (M=-0.05; 95%HDI=[-0.10,-0.002]). Note that this was not driven only by higher effort levels; even confining data to the lowest two effort levels, SHAPS has a predictive value for the proportion of accepted trials: M=-0.05; 95%HDI=[-0.07,-0.02].<br /> A visualisation of model agnostic task measures relating to symptoms is given in Fig. S4, comparing subgroups of participants scoring in the highest and lowest quartile on the SHAPS. This shows that participants with a high SHAPS score (i.e., more pronounced anhedonia) are less likely to accept offers than those with a low SHAPS score (Fig. S4A). Due to the implemented staircasing procedure, group differences can also be seen in the effort-reward combinations offered per trial. While for both groups, the staircasing procedure seems to devolve towards high effort – low reward offers, this is more pronounced in the subgroup of participants with a lower SHAPS score (Fig S4B).”

(3) None of the key effects relate to effort or reward sensitivity which is somewhat surprising given the previous literature and also means that it is hard to know if choice bias results would be equally found in tasks without any effort component. (The only analysis related to effort sensitivity is exploratory and in a subsample of N=56 per group looking at people meeting criteria for MDD vs matched controls.) Were stimuli constructed such that effort and reward sensitivity could be separated (i.e., are uncorrelated/orthogonal)? Maybe it would be worth looking at the % accepted in the largest or two largest effort value bins in an exploratory analysis. It seems the lowest and 2nd lowest effort level generally lead to accepting the challenge pretty much all the time, so including those effort levels might not be sensitive to individual difference analyses?

We too were initially surprised by the lack of effect of neuropsychiatric symptoms on reward and effort sensitivity. To address the Reviewer’s first comment, the nature of the ‘choice bias’ parameter (now motivational tendency) is its critical importance in the context of effort-based decision-making: it is not modelled or measured explicitly in tasks without effort (such as typical reward tasks), so it would be impossible to test this in tasks without an effort component. 

For the Reviewer’s second comment, the exploratory MDD analysis is not our only one related to effort sensitivity: the effort sensitivity parameter is included in all of our central analyses, and (like reward sensitivity), does not relate to our measured neuropsychiatric symptoms (e.g., see page 15). Note most previous effort tasks do not include a ‘choice bias’/motivational tendency parameter, potentially explaining this discrepancy. However, our model was quantitatively superior to models without this parameter, for example with only effort- and reward-sensitivity (page 11, Fig. 3).

Our three model parameters (reward sensitivity, effort sensitivity, and choice bias/motivational tendency) were indeed uncorrelated/orthogonal to one another (see parameter orthogonality analyses below), making it unlikely that the variance and effect captured by our motivational tendency parameter (previously termed “choice bias”) should really be attributed to reward sensitivity. As per the Reviewer’s suggestion, we also examined whether the lowest two effort levels might not be sensitive to individual differences; in fact, we found out proportion of accepted trials on the lowest effort levels alone was nevertheless predicted by anhedonia (see ceiling effect analyses below).

Specifically, in terms of parameter orthogonality:

When developing our task design and computational modelling approach we were careful to ensure that meaningful neurocomputational parameters could be estimated and that no spurious correlations between parameters would be introduced by modelling. By conducting parameter recoveries for all models, we showed that our modelling approach could reliably estimate parameters, and that estimated parameters are orthogonal to the other underlying parameters (as can be seen in Figure S1 in the supplement). It is thus unlikely that the variance and effect captured by our motivational tendency parameter (previously termed “choice bias”) should really be attributed to reward sensitivity.

And finally, regarding the possibility of a ceiling effect for low effort levels:

We agree that visual inspection of the proportion of accepted results across effort and reward values can lead to the belief that a ceiling effect prevents the two lowest effort levels from capturing any inter-individual differences. To test whether this is the case, we ran a Bayesian GLM with the SHAPS sum score predicting the proportion of accepted trials (controlling for age and gender), in a subset of the data including only trials with an effort level of 1 or 2. We found the SHAPS has a predictive value for the proportion of accepted trials in the lowest two effort levels: M=-0.05; 95%HDI=[-0.07,-0.02]). This is noted in the text as follows.

Supplement, lines 175 – 180:

“The proportion of accepted trials averaged across effort and reward levels was predicted by the Snaith-Hamilton Pleasure Scale (SHAPS) sum scores (M=-0.07; 95%HDI=[-0.12,-0.03]) and the Apathy Evaluation Scale (AES) sum scores (M=-0.05; 95%HDI=[-0.10,-0.002]). Note that this was not driven only by higher effort levels; even confining data to the lowest two effort levels, SHAPS has a predictive value for the proportion of accepted trials: M=-0.05; 95%HDI=[-0.07,-0.02].”

(4) The abstract and discussion seem overstated (implications for the school system and statements on circadian rhythms which were not measured here). They should be toned down to reflect conclusions supported by the data.

We thank the Reviewer for pointing this out, and have now removed these claims from the abstract and Discussion; we hope they now better reflect conclusions supported by these data directly.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) Suggestions for improved or additional experiments, data or analyses.

- For a non-computational audience, it would be useful to unpack the influence of the choice bias on behavior, as it is less clear how this would affect decision-making than sensitivity to effort or reward. Perhaps a figure showing accept/reject decisions when sensitivities are held and choice bias is high would be beneficial.

We thank the Reviewer for suggesting additional explanations of the choice bias parameter to aid interpretation for non-computational readers; as per the Reviewer’s suggestion, we have now included additional explanations and visualisations (Figure 3) to make this as clear as possible. Please note also that, in response to one of the other Reviewers and after careful considerations, we have decided to rename the “choice bias” parameter to “motivational tendency”, hoping this will prove more intuitive.

To aid with the understanding and interpretation of this and the other model parameters, we have added the following explanation to the main text.

Lines 149 – 155:

“The models posit efforts and rewards are joined into a subjective value (SV), weighed by individual effort (and reward sensitivity (parameters. The subjective value is then integrated with an individual motivational tendency (a) parameter to guide decision-making. Specifically, the motivational tendency parameter determines the range at which subjective values are translated to acceptance probabilities: the same subjective value will translate to a higher acceptance probability the higher the motivational tendency.”

Additionally, we add the following explanation to the Methods section.

Lines 698 – 709:

First, a cost function transforms costs and rewards associated with an action into a subjective value (SV):

with and for reward and effort sensitivity, and ℛ and 𝐸 for reward and effort. Higher effort and reward sensitivity mean the SV is more strongly influenced by changes in effort and reward, respectively (Fig. 3B-C). Hence, low effort and reward sensitivity mean the SV, and with that decision-making, is less guided by effort and reward offers, as would be in random decision-making.

This SV is then transformed to an acceptance probability by a softmax function:

with for the predicted acceptance probability and 𝛼 for the intercept representing motivational tendency. A high motivational tendency means a subjects has a tendency, or bias, to accept rather than reject offers (Fig. 3D).

Our new figure (panels A-D in figure 3) visualizes the model. This demonstrates how the different model parameters come at play in the model (A), and how different values on each parameter affects the model (B-D).

- The early and late chronotype groups have significant differences in ages and gender. Additional supplementary analysis here may mitigate any concerns from readers.

The Reviewer is right to notice that our subsamples of early and late chronotypes differ significantly in age and gender, but it important to note that all our analyses comparing these two groups take this into account, statistically controlling for age and gender. We regret that this was previously only mentioned in the Methods section, so this information was not accessible where most relevant. To remedy this, we have amended the Results section as follows.

Lines 317 – 323:

“Bayesian GLMs, controlling for age and gender, predicting task parameters by time-of-day and chronotype showed effects of chronotype on reward sensitivity (i.e. those with a late chronotype had a higher reward sensitivity; M= 0.325, 95% HDI=[0.19,0.46]) and motivational tendency (higher in early chronotypes; M=-0.248, 95% HDI=[-0.37,-0.11]), as well as an interaction between chronotype and time-of-day on motivational tendency (M=0.309, 95% HDI=[0.15,0.48]).”

(2) Recommendations for improving the writing and presentation.

- I found the term 'overlapping' a little jarring. I think the authors use it to mean both neuropsychiatric symptoms and chronotypes affect task parameters, but they are are not tested to be 'separable', nor is an interaction tested. Perhaps being upfront about how interactions are not being tested here (in the introduction, and not waiting until the discussion) would give an opportunity to operationalize this term.

We agree with the Reviewer that our previously-used term “overlapping” was not ideal: it may have been misleading, and was not necessarily reflective of the nature of our findings. We now state explicitly that we are not testing an interaction between neuropsychiatric symptoms and chronotypes in our primary analyses. Additionally, following suggestions made by Reviewer 3, we ran new exploratory analyses to investigate how the effects of neuropsychiatric symptoms and circadian measures on motivational tendency relate to one another. These results in fact show that all three symptom measures have separable effects from circadian measures on motivational tendency. This supports the Reviewer’s view that ‘overlapping’ was entirely the wrong word—although it nevertheless shows the important contribution of circadian rhythm as well as neuropsychiatric symptoms in effort-based decision-making. We have changed the manuscript throughout to better describe this important, more accurate interpretation of our findings, including replacing the term “overlapping”. We changed the title from “Overlapping effects of neuropsychiatric symptoms and circadian rhythm on effort-based decision-making” to “Both neuropsychiatric symptoms and circadian rhythm alter effort-based decision-making”.

To clarify the intention of our primary analyses, we have added the following to the last paragraph of the introduction.

Lines 107 – 112:

“Next, we pre-registered a follow-up experiment to directly investigate how circadian preference interacts with time-of-day on motivational decision-making, using the same task and computational modelling approach. While this allows us to test how circadian effects on motivational decision-making compare to neuropsychiatric effects, we do not test for possible interactions between neuropsychiatric symptoms and chronobiology.”

We detail our new analyses in the Methods section as follows.

Lines 800 – 814:

“4.5.2 Differentiating between the effects of neuropsychiatric symptoms and circadian measures on motivational tendency

To investigate how the effects of neuropsychiatric symptoms on motivational tendency (2.3.1) relate to effects of chronotype and time-of-day on motivational tendency we conducted exploratory analyses. In the subsamples of participants with an early or late chronotype (including additionally collected data), we first ran Bayesian GLMs with neuropsychiatric questionnaire scores (SHAPS, DARS, AES respectively) predicting motivational tendency, controlling for age and gender. We next added an interaction term of chronotype and time-of-day into the GLMs, testing how this changes previously observed neuropsychiatric and circadian effects on motivational tendency. Finally, we conducted a model comparison using LOO, comparing between motivational tendency predicted by a neuropsychiatric questionnaire, motivational tendency predicted by chronotype and time-of-day, and motivational tendency predicted by a neuropsychiatric questionnaire and time-of-day (for each neuropsychiatric questionnaire, and controlling for age and gender).”

Results of the outlined analyses are reported in the Results section as follows.

Lines 356 – 383:

“2.5.2.1 Neuropsychiatric symptoms and circadian measures have separable effects on motivational tendency

Exploratory analyses testing for the effects of neuropsychiatric questionnaires on motivational tendency in the subsamples of early and late chronotypes confirmed the predictive value of the SHAPS (M=-0.24, 95% HDI=[-0.42,-0.06]), the DARS (M=-0.16, 95% HDI=[-0.31,-0.01]), and the AES (M=-0.18, 95% HDI=[-0.32,-0.02]) on motivational tendency.

For the SHAPS, we find that when adding the measures of chronotype and time-of-day back into the GLMs, the main effect of the SHAPS (M=-0.26, 95% HDI=[-0.43,-0.07]), the main effect of chronotype (M=-0.11, 95% HDI=[-0.22,-0.01]), and the interaction effect of chronotype and time-of-day (M=0.20, 95% HDI=[0.07,0.34]) on motivational tendency remain. Model comparison by LOOIC reveals motivational tendency is best predicted by the model including the SHAPS, chronotype and time-of-day as predictors, followed by the model including only the SHAPS. Note that this approach to model comparison penalizes models for increasing complexity.

Repeating these steps with the DARS, the main effect of the DARS is found numerically, but the 95% HDI just includes 0 (M=-0.15, 95% HDI=[-0.30,0.002]). The main effect of chronotype (M=-0.11, 95% HDI=[-0.21,-0.01]), and the interaction effect of chronotype and time-of-day (M=0.18, 95% HDI=[0.05,0.33]) on motivational tendency remain. Model comparison identifies the model including the DARS and circadian measures as the best model, followed by the model including only the DARS.

For the AES, the main effect of the AES is found (M=-0.19, 95% HDI=[-0.35,-0.04]). For the main effect of chronotype, the 95% narrowly includes 0 (M=-0.10, 95% HDI=[-0.21,0.002]), while the interaction effect of chronotype and time-of-day (M=0.20, 95% HDI=[0.07,0.34]) on motivational tendency remains. Model comparison identifies the model including the AES and circadian measures as the best model, followed by the model including only the AES.”

In addition to the title change, we edited our Discussion to discuss and reflect these new insights, including the following.

Lines 399 – 402:

“Various neuropsychiatric disorders are marked by disruptions in circadian rhythm, such as a late chronotype. However, research has rarely investigated how transdiagnostic mechanisms underlying neuropsychiatric conditions may relate to inter-individual differences in circadian rhythm.”

Lines 475 – 480:

“It is striking that the effects of neuropsychiatric symptoms on effort-based decision-making largely are paralleled by circadian effects on the same neurocomputational parameter. Exploratory analyses predicting motivational tendency by neuropsychiatric symptoms and circadian measures simultaneously indicate the effects go beyond recapitulating each other, but rather explain separable parts of the variance in motivational tendency.”

Lines 528 – 532:

“Our reported analyses investigating neuropsychiatric and circadian effects on effort-based decision-making simultaneously are exploratory, as our study design was not ideally set out to examine this. Further work is needed to disentangle separable effects of neuropsychiatric and circadian measures on effort-based decision-making.”

Lines 543 – 550:

“We demonstrate that neuropsychiatric effects on effort-based decision-making are paralleled by effects of circadian rhythm and time-of-day. Exploratory analyses suggest these effects account for separable parts of the variance in effort-based decision-making. It unlikely that effects of neuropsychiatric effects on effort-based decision-making reported here and in previous literature are a spurious result due to multicollinearity with chronotype. Yet, not accounting for chronotype and time of testing, which is the predominant practice in the field, could affect results.”

- A minor point, but it could be made clearer that many neurotransmitters have circadian rhythms (and not just dopamine).

We agree this should have been made clearer, and have added the following to the Introduction.

Lines 83 – 84:

“Bi-directional links between chronobiology and several neurotransmitter systems have been reported, including dopamine47.

(47) Kiehn, J.-T., Faltraco, F., Palm, D., Thome, J. & Oster, H. Circadian Clocks in the Regulation of Neurotransmitter Systems. Pharmacopsychiatry 56, 108–117 (2023).”

- Making reference to other studies which have explored circadian rhythms in cognitive tasks would allow interested readers to explore the broader field. One such paper is: Bedder, R. L., Vaghi, M. M., Dolan, R. J., & Rutledge, R. B. (2023). Risk taking for potential losses but not gains increases with time of day. Scientific reports, 13(1), 5534, which also includes references to other similar studies in the discussion.

We thank the Reviewer for pointing out that we failed to cite this relevant work. We have now included it in the Introduction as follows.

Lines 97 – 98:

“A circadian effect on decision-making under risk is reported, with the sensitivity to losses decreasing with time-of-day66.

(66) Bedder, R. L., Vaghi, M. M., Dolan, R. J. & Rutledge, R. B. Risk taking for potential losses but not gains increases with time of day. Sci Rep 13, 5534 (2023).”

(3) Minor corrections to the text and figures.

None, clearly written and structured. Figures are high quality and significantly aid understanding.

Reviewer #2 (Recommendations For The Authors):

I did have a few more minor comments:

- The manuscript doesn't clarify whether trials had time limits - so that participants might fail to earn points - or instead they did not and participants had to continue exerting effort until they were done. This is important to know since it impacts on decision-strategies and behavioral outcomes that might be analyzed. For example, if there is no time limit, it might be useful to examine the amount of time it took participants to complete their effort - and whether that had any relationship to choice patterns or symptomatology. Or, if they did, it might be interesting to test whether the relationship between choices and exerted effort depended on symptoms. For example, someone with depression might be less willing to choose effort, but just as, if not more likely to successfully complete a trial once it is selected.

We thank the Reviewer for pointing out this important detail in the task design, which we should have made clearer. The trials did indeed have a time limit which was dependent on the effort level. To clarify this in the manuscript, we have made changes to Figure 2 and the Methods section. We agree it would be interesting to explore whether the exerted effort in the task related to symptoms. We explored this in our data by predicting the participant average proportion of accepted but failed trials by SHAPS score (controlling for age and gender). We found no relationship: M=0.01, 95% HDI=[-0.001,0.02]. However, it should be noted that the measure of proportion of failed trials may not be suitable here, as there are only few accepted but failed trials (M = 1.3% trials failed, SD = 3.50). This results from several task design characteristics aimed at preventing subjects from failing accepted trials, to avoid confounding of effort discounting with risk discounting. As an alternative measure, we explored the extent to which participants went “above and beyond” the target in accepted trials. Specifically, considering only accepted and succeeded trials, we computed the factor by which the required number of clicks was exceeded (i.e., if a subject clicked 15 times when 10 clicks were required the factor would be 1.3), averaging across effort and reward level. We then conducted a Bayesian GLM to test whether this subject wise click-exceedance measure can be predicted by apathy or anhedonia, controlling for age and gender. We found neither the SHAPS (M=-0.14, 95% HDI=[-0.43,0.17]) nor the AES (M=0.07, 95% HDI=[-0.26,0.41]) had a predictive value for the amount to which subjects exert “extra effort”. We have now added this to the manuscript.

In Figure 2, which explains the task design in the results section, we have added the following to the figure description.

Lines 161 – 165:

“Each trial consists of an offer with a reward (2,3,4, or 5 points) and an effort level (1,2,3, or 4, scaled to the required clicking speed and time the clicking must be sustained for) that subjects accept or reject. If accepted, a challenge at the respective effort level must be fulfilled for the required time to win the points.”

In the Methods section, we have added the following.

Lines 617 – 622:

“We used four effort-levels, corresponding to a clicking speed at 30% of a participant’s maximal capacity for 8 seconds (level 1), 50% for 11 seconds (level 2), 70% for 14 seconds (level 3), and 90% for 17 seconds (level 4). Therefore, in each trial, participants had to fulfil a certain number of mouse clicks (dependent on their capacity and the effort level) in a specific time (dependent on the effort level).”

In the Supplement, we have added the additional analyses suggested by the Reviewer.

Lines 195 – 213:

“3.2 Proportion of accepted but failed trials

For each participant, we computed the proportion of trial in which an offer was accepted, but the required effort then not fulfilled (i.e., failed trials). There was no relationship between average proportion of accepted but failed trials and SHAPS score (controlling for age and gender): M=0.01, 95% HDI=[-0.001,0.02]. However, there are intentionally few accepted but failed trials (M = 1.3% trials failed, SD = 3.50). This results from several task design characteristics aimed at preventing subjects from failing accepted trials, to avoid confounding of effort discounting with risk discounting.”

“3.3 Exertion of “extra effort”

We also explored the extent to which participants went “above and beyond” the target in accepted trials. Specifically, considering only accepted and succeeded trials, we computed the factor by which the required number of clicks was exceeded (i.e., if a subject clicked 15 times when 10 clicks were required the factor would be 1.3), averaging across effort and reward level. We then conducted a Bayesian GLM to test whether this subject wise click-exceedance measure can be predicted by apathy or anhedonia, controlling for age and gender. We found neither the SHAPS (M=-0.14, 95% HDI=[-0.43,0.17]) nor the AES (M=0.07, 95% HDI=[-0.26,0.41]) had a predictive value for the amount to which subjects exert “extra effort”.”

- Perhaps relatedly, there is evidence that people with depression show less of an optimism bias in their predictions about future outcomes. As such, they show more "rational" choices in probabilistic decision tasks. I'm curious whether the Authors think that a weaker choice bias among those with stronger depression/anhedonia/apathy might be related. Also, are choices better matched with actual effort production among those with depression?

We think this is a very interesting comment, but unfortunately feel our manuscript cannot properly speak to it: as in our response to the previous comment, our exploratory analysis linking the proportion of accepted but failed trials to anhedonia symptoms (i.e. less anhedonic people making more optimistic judgments of their likelihood of success) did not show a relationship between the two. However, this null finding may be the result of our task design which is not laid out to capture such an effect (in fact to minimize trials of this nature). We have added to the Discussion section.

Lines 442 – 445:

“It is possible that a higher motivational tendency reflects a more optimistic assessment of future task success, in line with work on the optimism bias95; however our task intentionally minimized unsuccessful trials by titrating effort and reward; future studies should explore this more directly.

(95) Korn, C. W., Sharot, T., Walter, H., Heekeren, H. R. & Dolan, R. J. Depression is related to an absence of optimistically biased belief updating about future life events. Psychological Medicine 44, 579–592 (2014).”

- The manuscript does not clarify: How did the Authors ensure that each subject received each effort-reward combination at least once if a given subject always accepted or always rejected offers?

We have made the following edit to the Methods section to better explain this aspect of our task design.

Lines 642 – 655:

“For each subject, trial-by-trial presentation of effort-reward combinations were made semi-adaptively by 16 randomly interleaved staircases. Each of the 16 possible offers (4 effort-levels x 4 reward-levels) served as the starting point of one of the 16 staircase. Within each staircase, after a subject accepted a challenge, the next trial’s offer on that staircase was adjusted (by increasing effort or decreasing reward). After a subject rejected a challenge, the next offer on that staircase was adjusted by decreasing effort or increasing reward. This ensured subjects received each effort-reward combination at least once (as each participant completed all 16 staircases), while individualizing trial presentation to maximize the trials’ informative value. Therefore, in practice, even in the case of a subject rejecing all offers (and hence the staircasing procedures always adapting by decreasing effort or increasing reward), the full range of effort-reward combinations will be represented in the task across the startingpoints of all staircases (and therefore before adaption takeplace).”

- The word "metabolic" is misspelled in Table 1

- Figure 2 is missing panel label "C"

- The word "effort" is repeated on line 448.

We thank the Reviewer for their attentive reading of our manuscript and have corrected the mistakes mentioned.

Reviewer #3 (Recommendations For The Authors):

It is a bit difficult to get a sense of people's discounting from the plots provided. Could the authors show a few example individuals and their fits (i.e., how steep was effort discounting on average and how much variance was there across individuals; maybe they could show the mean discount function or some examples etc)

We appreciate very much the Reviewer's suggestion to visualise our parameter estimates within and across individuals. We have implemented this in Figure .S2

It would be helpful if correlations between the various markers used as dependent variables (SHAPS, DARS, AES, chronotype etc) could plotted as part of each related figure (e.g., next to the relevant effects shown).

We agree with the Reviewer that a visual representation of the various correlations between dependent variables would be a better and more assessable communication than our current paragraph listing the correlations. We have implemented this by adding a new figure plotting all correlations in a heat map, with asterisks indicating significance.

The authors use the term "meaningful relationship" - how is this defined? If undefined, maybe consider changing (do they mean significant?)

We understand how our use of the term “(no) meaningful relationship” was confusing here. As we conducted most analyses in a Bayesian fashion, this is a formal definition of ‘meaningful’: the 95% highest density interval does not span across 0. However, we do not want this to be misunderstood as frequentist “significance” and agree clarity can be improved here, To avoid confusion, we have amended the manuscript where relevant (i.e., we now state “we found a (/no) relationship / effect” rather than “we found a meaningful relationship”.

The authors do not include an inverse temperature parameter in their discounting models-can they motivate why? If a participant chose nearly randomly, which set of parameter values would they get assigned?

Our decision to not include an inverse temperature parameter was made after an extensive simulation-based investigation of different models and task designs. A series of parameter recovery studies including models with an inverse temperature parameter revealed the inverse temperature parameter could not be distinguished from the reward sensitivity parameter. Specifically, inverse temperature seemed to capture the variance of the true underlying reward sensitivity parameter, leading to confounding between the two. Hence, including both reward sensitivity and inverse temperature would not have allowed us to reliably estimate either parameter. As our pre-registered hypotheses related to the reward sensitivity parameter, we opted to include models with the reward sensitivity parameter rather than the inverse temperature parameter in our model space. We have now added these simulations to our supplement.

Nevertheless, we believe our models can capture random decision-making. The parameters of effort and reward sensitivity capture how sensitive one is to changes in effort/reward level. Hence, random decision-making can be interpreted as low effort and reward sensitivity, such that one’s decision-making is not guided by changes in effort and reward magnitude. With low effort/reward sensitivity, the motivational tendency parameter (previously “choice bias”) would capture to what extend this random decision-making is biased toward accepting or rejecting offers.

The simulation results are now detailed in the Supplement.

Lines 25 – 46:

“1.2.1 Parameter recoveries including inverse temperature

In the process of task and model space development, we also considered models incorportating an inverse temperature paramater. To this end, we conducted parameter recoveries for four models, defined in Table S3.

Parameter recoveries indicated that, parameters can be recovered reliably in model 1, which includes only effort sensitivity ( ) and inverse temperature as free parameters (on-diagonal correlations: .98 > r > .89, off-diagonal correlations: .04 > |r| > .004). However, as a reward sensitivity parameter is added to the model (model 2), parameter recovery seems to be compromised, as parameters are estimated less accurately (on-diagonal correlations: .80 > r > .68), and spurious correlations between parameters emerge (off-diagonal correlations: .40 > |r| > .17). This issue remains when motivational tendency is added to the model (model 4; on-diagonal correlations: .90 > r > .65; off-diagonal correlations: .28 > |r| > .03), but not when inverse temperature is modelled with effort sensitivity and motivational tendency, but not reward sensitivity (model 3; on-diagonal correlations: .96 > r > .73; off-diagonal correlations: .05 > |r| > .003).

As our pre-registered hypotheses related to the reward sensitivity parameter, we opted to include models with the reward sensitivity parameter rather than the inverse temperature parameter in our model space.”

And we now discuss random decision-making specifically in the Methods section.

Lines 698 – 709:

“First, a cost function transforms costs and rewards associated with an action into a subjective value (SV):

with and for reward and effort sensitivity, and  and  for reward and effort. Higher effort and reward sensitivity mean the SV is more strongly influenced by changes in effort and reward, respectively (Fig. 3B-C). Hence, low effort and reward sensitivity mean the SV, and with that decision-making, is less guided by effort and reward offers, as would be in random decision-making.

This SV is then transformed to an acceptance probability by a softmax function:

with for the predicted acceptance probability and  for the intercept representing motivational tendency. A high motivational tendency means a subjects has a tendency, or bias, to accept rather than reject offers (Fig. 3D).”

The pre-registration mentions effects of BMI and risk of metabolic disease-those are briefly reported the in factor loadings, but not discussed afterwards-although the authors stated hypotheses regarding these measures in their preregistration. Were those hypotheses supported?

We reported these results (albeit only briefly) in the factor loadings resulting from our PLS regression and results from follow-up GLMs (see below). We have now amended the Discussion to enable further elaboration on whether they confirmed our hypotheses (this evidence was unclear, but we have subsequently followed up in a sample with type-2 diabetes, who also show reduced motivational tendency).

Lines 258 – 261:

“For the MEQ (95%HDI=[-0.09,0.06]), MCTQ (95%HDI=[-0.17,0.05]), BMI (95%HDI=[-0.19,0.01]), and FINDRISC (95%HDI=[-0.09,0.03]) no relationship with motivational tendency was found, consistent with the smaller magnitude of reported component loadings from the PLS regression.”

We have added the following paragraph to our discussion.

Lines 491 – 502:

“To our surprise, we did not find statistical evidence for a relationship between effort-based decision-making and measures of metabolic health (BMI and risk for type-2 diabetes). Our analyses linking BMI to motivational tendency reveal a numeric effect in line with our hypothesis: a higher BMI relating to a lower motivational tendency. However, the 95% HDI for this effect narrowly included zero (95%HDI=[-0.19,0.01]). Possibly, our sample did not have sufficient variance in metabolic health to detect dimensional metabolic effects in a current general population sample. A recent study by our group investigates the same neurocomputational parameters of effort-based decision-making in participants with type-2 diabetes and non-diabetic controls matched by age, gender, and physical activity105. We report a group effect on the motivational tendency parameter, with type-2 diabetic patients showing a lower tendency to exert effort for reward.”

“(105) Mehrhof, S. Z., Fleming, H. A. & Nord, C. A cognitive signature of metabolic health in effort-based decision-making. Preprint at https://doi.org/10.31234/osf.io/4bkm9 (2024).”

R-values are indicated as a range (e.g., from 0.07-0.72 for the last one in 2.1 which is a large range). As mentioned above, the full correlation matrix should be reported in figures as heatmaps.

We agree with the Reviewer that a heatmap is a better way of conveying this information – see Figure 1 in response to their previous comment.  

The answer on whether data was already collected is missing on the second preregistration link. Maybe this is worth commenting on somewhere in the manuscript.

This question appears missing because, as detailed in the manuscript, we felt that technically some data *was* already collected by the time our second pre-registration was posted. This is because the second pre-registration detailed an additional data collection, with the goal of extending data from the original dataset to include extreme chronotypes and increase precision of analyses. To avoid any confusion regarding the lack of reply to this question in the pre-registration, we have added the following disclaimer to the description of the second pre-registration:

“Please note the lack of response to the question regarding already collected data. This is because the data collection in the current pre-registration extends data from the original dataset to increase the precision of analyses. While this original data is already collected, none of the data collection described here has taken place.”

Some referencing is not reflective of the current state of the field (e.g., for effort discounting: Sugiwaka et al., 2004 is cited). There are multiple labs that have published on this since then including Philippe Tobler's and Sven Bestmann's groups (e.g., Hartmann et al., 2013; Klein-Flügge et al., Plos CB, 2015).

We agree absolutely, and have added additional, more recent references on effort discounting.

Lines 67 – 68:

“Higher costs devalue associated rewards, an effect referred to as effort-discounting33–37.”

(33) Sugiwaka, H. & Okouchi, H. Reformative self-control and discounting of reward value by delay or effort1. Japanese Psychological Research 46, 1–9 (2004).

(34) Hartmann, M. N., Hager, O. M., Tobler, P. N. & Kaiser, S. Parabolic discounting of monetary rewards by physical effort. Behavioural Processes 100, 192–196 (2013).

(35) Klein-Flügge, M. C., Kennerley, S. W., Saraiva, A. C., Penny, W. D. & Bestmann, S. Behavioral Modeling of Human Choices Reveals Dissociable Effects of Physical Effort and Temporal Delay on Reward Devaluation. PLOS Computational Biology 11, e1004116 (2015).

(36) Białaszek, W., Marcowski, P. & Ostaszewski, P. Physical and cognitive effort discounting across different reward magnitudes: Tests of discounting models. PLOS ONE 12, e0182353 (2017).

(37) Ostaszewski, P., Bąbel, P. & Swebodziński, B. Physical and cognitive effort discounting of hypothetical monetary rewards. Japanese Psychological Research 55, 329–337 (2013).

There are lots of typos throughout (e.g., Supplementary martial, Mornignness etc)

We thank the Reviewer for their attentive reading of our manuscript and have corrected our mistakes.

In Table 1, it is not clear what the numbers given in parentheses are. The figure note mentions SD, IQR, and those are explicitly specified for some rows, but not all.

After reviewing Table 1 we understand the comment regarding the clarity of the number in parentheses. In our original manuscript, for some variables, numbers were given per category (e.g. for gender and ethnicity), rather than per row, in which case the parenthetical statistic was indicated in the header row only. However, we now see that the clarity of the table would have been improved by adding the reported statistic for each row—we have corrected this.

In Figure 1C, it would be much more helpful if the different panels were combined into one single panel (using differently coloured dots/lines instead of bars).

We agree visualizing the proportion of accepted trials across effort and reward levels in one single panel aids interpretability. We have implemented it in the following plot (now Figure 2C).

In Sections 2.2.1 and 4.2.1, the authors mention "mixed-effects analysis of variance (ANOVA) of repeated measures" (same in the preregistration). It is not clear if this is a standard RM-ANOVA (aggregating data per participant per condition) or a mixed-effects model (analysing data on a trial-by-trial level). This model seems to only include within-subjects variable, so it isn't a "mixed ANOVA" mixing within and between subjects effects.

We apologise that our use of the term "mixed-effects analysis of variance (ANOVA) of repeated measures" is indeed incorrectly applied here. We aggregate data per participant and effort-by-reward combination, meaning there are no between-subject effects tested. We have corrected this to “repeated measures ANOVA”.

In Section 2.2.2, the authors write "R-hats>1.002" but probably mean "R-hats < 1.002". ESS is hard to evaluate unless the total number of samples is given.

We thank the Reviewer for noticing this mistake and have corrected it in the manuscript.

In Section 2.3, the inference criterion is unclear. The authors first report "factor loadings" and then perform a permutation test that is not further explained. Which of these factors are actually needed for predicting choice bias out of chance? The permutation test suggests that the null hypothesis is just "none of these measures contributes anything to predicting choice bias", which is already falsified if only one of them shows an association with choice bias. It would be relevant to know for which measures this is the case. Specifically, it would be relevant to know whether adding circadian measures into a model that already contains apathy/anhedonia improves predictive performance.

We understand the Reviewer’s concerns regarding the detail of explanation we have provided for this part of our analysis, but we believe there may have been a misunderstanding regarding the partial least squares (PLS) regression. Rather than identifying a number of factors to predict the outcome variable, a PLS regression identifies a model with one or multiple components, with various factor loadings of differing magnitude. In our case, the PLS regression identified a model with one component to best predict our outcome variable (motivational tendency, which in our previous various we called choice bias). This one component had factor loadings of our questionnaire-based measures, with measures of apathy and anhedonia having highest weights, followed by lesser weighted factor loadings by measures of circadian rhythm and metabolic health. The permutation test tests whether this component (consisting of the combination of factor loadings) can predict the outcome variable out of sample.

We hope we have improved clarity on this in the manuscript by making the following edits to the Results section.

Lines 248 – 251:

“Permutation testing indicated the predictive value of the resulting component (with factor loadings described above) was significant out-of-sample (root-mean-squared error [RMSE]=0.203, p=.001).”

Further, we hope to provide a more in-depth explanation of these results in the Methods section.

Lines 755 – 759:

“Statistical significance of obtained effects (i.e., the predictive accuracy of the identified component and factor loadings) was assessed by permutation tests, probing the proportion of root-mean-squared errors (RMSEs) indicating stronger or equally strong predictive accuracy under the null hypothesis.”

In Section 2.5, the authors simply report "that chronotype showed effects of chronotype on reward sensitivity", but the direction of the effect (higher reward sensitivity in early vs. late chronotype) remains unclear.

We thank the Reviewer for pointing this out. While we did report the direction of effect, this was only presented in the subsequent parentheticals and could have been made much clearer. To assist with this, we have made the following addition to the text.

Lines 317 – 320:

“Bayesian GLMs, controlling for age and gender, predicting task parameters by time-of-day and chronotype showed effects of chronotype on reward sensitivity (i.e. those with a late chronotype had a higher reward sensitivity; M= 0.325, 95% HDI=[0.19,0.46])”

In Section 4.2, the authors write that they "implemented a previously-described procedure using Prolific pre-screeners", but no reference to this previous description is given.

We thank the Reviewer for bringing our attention to this missing reference, which has now been added to the manuscript.

In Supplementary Table S2, only the "on-diagonal correlations" are given, but off-diagonal correlations (indicative of trade-offs between parameters) would also be informative.

We agree with the Reviewer that off-diagonal correlations between underlying and recovered parameters are crucial to assess confounding between parameters during model estimation. We reported this in figure S1D, where we present the full correlation matric between underlying and recovered parameters in a heatmap. We have now noticed that this plot was missing axis labels, which have been added now.

I found it somewhat difficult to follow the results section without having read the methods section beforehand. At the beginning of the Results section, could the authors briefly sketch the outline of their study? Also, given they have a pre-registration, could the authors introduce each section with a statement of what they expected to find, and close with whether the data confirmed their expectations? In the current version of the manuscript, many results are presented without much context of what they mean.

We agree a brief outline of the study procedure before reporting the results would be beneficial to following the subsequently text and have added the following to the end of our Introduction.

Lines 101 – 106:

“Here, we tested the relationship between motivational decision-making and three key neuropsychiatric syndromes: anhedonia, apathy, and depression, taking both a transdiagnostic and categorical (diagnostic) approach. To do this, we validate a newly developed effort-expenditure task, designed for online testing, and gamified to increase engagement. Participants completed the effort-expenditure task online, followed by a series of self-report questionnaires.”

We have added references to our pre-registered hypotheses at multiple points in our manuscript.

Lines 185 – 187:

“In line with our pre-registered hypotheses, we found significant main effects for effort (F(1,14367)=4961.07, p<.0001) and reward (F(1,14367)=3037.91, p<.001), and a significant interaction between the two (F(1,14367)=1703.24, p<.001).”

Lines 215 – 221:

“Model comparison by out-of-sample predictive accuracy identified the model implementing three parameters (motivational tendency a, reward sensitivity , and effort sensitivity ), with a parabolic cost function (subsequently referred to as the full parabolic model) as the winning model (leave-one-out information criterion [LOOIC; lower is better] = 29734.8; expected log posterior density [ELPD; higher is better] = -14867.4; Fig. 31ED). This was in line with our pre-registered hypotheses.”

Lines 252 – 258:

“Bayesian GLMs confirmed evidence for psychiatric questionnaire measures predicting motivational tendency (SHAPS: M=-0.109; 95% highest density interval (HDI)=[-0.17,-0.04]; AES: M=-0.096; 95%HDI=[-0.15,-0.03]; DARS: M=-0.061; 95%HDI=[-0.13,-0.01]; Fig. 4A). Post-hoc GLMs on DARS sub-scales showed an effect for the sensory subscale (M=-0.050; 95%HDI=[-0.10,-0.01]). This result of neuropsychiatric symptoms predicting a lower motivational tendency is in line with our pre-registered hypothesis.”

Lines 258 – 263:

“For the MEQ (95%HDI=[-0.09,0.06]), MCTQ (95%HDI=[-0.17,0.05]), BMI (95%HDI=[-0.19,0.01]), and FINDRISC (95%HDI=[-0.09,0.03]) no meaningful relationship with choice biasmotivational tendency was found, consistent with the smaller magnitude of reported component loadings from the PLS regression. This null finding for dimensional measures of circadian rhythm and metabolic health was not in line with our pre-registered hypotheses.”

Lines 268 – 270:

“For reward sensitivity, the intercept-only model outperformed models incorporating questionnaire predictors based on RMSE. This result was not in line with our pre-registered expectations.”

Lines 295 – 298:

“As in our transdiagnostic analyses of continuous neuropsychiatric measures (Results 2.3), we found evidence for a lower motivational tendency parameter in the MDD group compared to HCs (M=-0.111, 95% HDI=[ -0.20,-0.03]) (Fig. 4B). This result confirmed our pre-registered hypothesis.”

Lines 344 – 355:

“Late chronotypes showed a lower motivational tendency than early chronotypes (M=-0.11, 95% HDI=[-0.22,-0.02])—comparable to effects of transdiagnostic measures of apathy and anhedonia, as well as diagnostic criteria for depression. Crucially, we found motivational tendency was modulated by an interaction between chronotype and time-of-day (M=0.19, 95% HDI=[0.05,0.33]): post-hoc GLMs in each chronotype group showed this was driven by a time-of-day effect within late, rather than early, chronotype participants (M=0.12, 95% HDI=[0.02,0.22], such that late chronotype participants showed a lower motivational tendency in the morning testing sessions, and a higher motivational tendency in the evening testing sessions; early chronotype: 95% HDI=[-0.16,0.04]) (Fig. 5A). These results of a main effect and an interaction effect of chronotype on motivational tendency confirmed our pre-registered hypothesis.”

Lines 390 – 393:

“Participants with an early chronotype had a lower reward sensitivity parameter than those with a late chronotype (M=0.27, 95% HDI=[0.16,0.38]). We found no effect of time-of-day on reward sensitivity (95%HDI=[-0.09,0.11]) (Fig. 5B). These results were in line with our pre-registered hypotheses.”

Author response:

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

Reviewer #1 (Public Review):

Comments on revisions:

This revision addressed all my previous comments.

Reviewer #3 (Public Review):

Comments on revisions:

The authors addressed my comments and it is ready for publication.

We are grateful for the reviewers’ effort and are encouraged by their generally positive assessment of our manuscript.

Reviewer #1 (Recommendations For The Authors):

This revision addressed all my previous comments. The only new issue concerns the authors’ response to the following comment of reviewer 3:

(2) Authors note ”monovalent positive salt ions such as Na+ can be attracted, somewhat counterintuitively, into biomolecular condensates scaffolded by positively-charged polyelectrolytic IDRs in the presence of divalent counterions”. This may be due to the fact that the divalent negative counterions present in the dense phase (as seen in the ternary phase diagrams) also recruit a small amount of Na+.

Author reply: The reviewer’s comment is valid, as a physical explanation for this prediction is called for. Accordingly, the following sentence is added to p. 10, lines 27-29: ...

Here are my comments on this issue. Most IDPs with a net positive charge still have negatively charged residues, which in theory can bind cations. In fact, Caprin1 has 3 negatively charged residues (same as A1-LCD). All-atom simulations of MacAinsh et al (ref 72) have shown that these negatively charged residues bind Na+; I assume this effect can be captured by the coarsegrained models in the present study. Moreover, all-atom simulations showed that Na+ has a strong tendency to be coordinated by backbone carbonyls, which of course are present on all residues. Suggestions:

(a) The authors may want to analyze the binding partners of Na+. Are they predominantly the3 negatively charged residues, or divalent counterions, or both?

(b) The authors may want to discuss the potential underestimation of Na+ inside Caprin1 condensates due to the lack of explicit backbone carbonyls that can coordinate Na+ in their models. A similar problem applies to backbone amides that can coordinate anions, but to a lesser extent (see Fig. 3A of ref 72).

The reviewer’s comments are well taken. Regarding the statement in the revised manuscript “This phenomenon arises because the positively charge monovalent salt ions are attracted to the negatively charged divalent counterions in the protein-condensed phase.”, it should be first noted that the statement was inferred from the model observation that Na+ is depleted in condensed Caprin1 (Fig. 2a) when the counterion is monovalent (an observation that was stated almost immediately preceding the quoted statement). To make this logical connection clearer as well as to address the reviewer’s point about the presence of negatively charged residues in Caprin1, we have modified this statement in the Version of Record (VOR) as follows:

“This phenomenon most likely arises from the attraction of the positively charge monovalent salt ions to the negatively charged divalent counterions in the proteincondensed phase because although the three negatively charged D residues in Caprin1 can attract Na+, it is notable that Na+ is depleted in condensed Caprin1 when the counterion is monovalent (Fig. 2a).”

The reviewer’s suggestion (a) of collecting statistics of Na+ interactions in the Caprin1 condensate is valuable and should be attempted in future studies since it is beyond the scope of the present work. Thus far, our coarse-grained molecular dynamics has considered only monovalent Cl− counterions. We do not have simulation data for divalent counterions.

Following the reviewer’s suggestion (b), we have now added the following sentence in Discussion under the subheading “Effects of salt on biomolecular LLPS”:

“In this regard, it should be noted that positively and negatively charged salt ions can also coordinate with backbone carbonyls and amides, respectively, in addition to coordinating with charged amino acid sidechains (MacAinsh et al., eLife 2024). The impact of such effects, which are not considered in the present coarse-grained models, should be ascertained by further investigations using atomic simulations (MacAinsh et al., eLife 2024; Rauscher & Pom`es, eLife 2017; Zheng et al., J Phys Chem B 2020).”

Here we have added a reference to Rauscher & Pom`es, eLife 2017 to more accurately reflect progress made in atomic simulations of biomolecular condensates.

More generally, regarding the reviewer’s comments on the merits of coarse-grained versus atomic approaches, we re-emphasize, as stated in our paper, that these approaches are complementary. Atomic approaches undoubtedly afford structurally and energetically high-resolution information. However, as it stands, simulations of the assembly-disassembly process of biomolecular condensate are nonideal because of difficulties in achieving equilibration even for a small model system with < 10 protein chains (MacAinsh et al., eLife 2024) although well-equilibrated simulations are possible for a reasonably-sized system with ∼ 30 chains when the main focus is on the condensed phase (Rauscher & Pom`es, eLife 2017). In this context, coarse-grained models are valuable for assessing the energetic role of salt ions in the thermodynamic stability of biomolecular condensates of physically reasonable sizes under equilibrium conditions.

In addition to the above minor additions, we have also added citations in the VOR to two highly relevant recent papers: Posey et al., J Am Chem Soc 2024 for salt-dependent biomolecular condensation (mentioned in Dicussion under subheadings “Tielines in protein-salt phase diagrams” and “Counterion valency” together with added references to Hribar et al., J Am Chem Soc 2002 and Nostro & Ninham, Chem Rev 2012 for the Hofmeister phenomena discussed by Posey et al.) and Zhu et al., J Mol Cell Biol 2024 for ATP-modulated reentrant behavior (mentioned in Introduction). We have also added back a reference to our previous work Lin et al., J Mol Liq 2017 to provide more background information for our formulation.

Reviewer #2 (Recommendations For The Authors):

The authors have done a great job addressing previous comments.

We thank this reviewer for his/her effort and are encouraged by the positive assessment of our revised manuscript.

---

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

Reviewer #1 (Public Review):

Summary:

The authors used multiple approaches to study salt effects in liquid-liquid phase separation (LLPS). Results on both wild-type Caprin1 and mutants and on different types of salts contribute to a comprehensive understanding.

Strengths:

The main strength of this work is the thoroughness of investigation. This aspect is highlighted by the multiple approaches used in the study, and reinforced by the multiple protein variants and different salts studied.

We are encouraged by this positive overall assessment.

Weaknesses: (1) The multiple computational approaches are a strength, but they’re cruder than explicit-solvent all-atom molecular dynamics (MD) simulations and may miss subtle effects of salts. In particular, all-atom MD simulations demonstrate that high salt strengthens pi-types of interactions (ref. 42 and MacAinsh et al, https://www.biorxiv.org/content/10.1101/2024.05.26.596000v3).

The relative strengths and limitations of coarse-grained vs all-atom simulation are now more prominently discussed beginning at the bottom of p. 5 through the first 8 lines of p. 6 of the revised manuscript (page numbers throughout this letter refer to those in the submitted pdf file of the revised manuscript), with MacAinsh et al. included in this added discussion (cited as ref. 72 in the revised manuscript). The fact that coarse-grained simulation may not provide insights into more subtle structural and energetic effects afforded by all-atom simulations with regard to π-related interaction is now further emphasized on p. 11 (lines 23–30), with reference to MacAinsh et al. as well as original ref. 42 (Krainer et al., now ref. 50 in the revised manuscript).

(2) The paper can be improved by distilling the various results into a simple set of conclusions. By example, based on salt effects revealed by all-atom MD simulations, MacAinsh et al. presented a sequence-based predictor for classes of salt dependence. Wild-type Caprin1 fits right into the “high net charg”e class, with a high net charge and a high aromatic content, showing no LLPS at 0 NaCl and an increasing tendency of LLPS with increasing NaCl. In contrast, pY-Caprin1 belongs to the “screening” class, with a high level of charged residues and showing a decreasing tendency of LLPS.

This is a helpful suggestion. We have now added a subsection with heading “Overview of key observations from complementary approaches” at the beginning of the “Results” section on p. 6 (lines 18–37) and the first line of p. 7. In the same vein, a few concise sentences to summarize our key results are added to the first paragraph of “Discussion” (p. 18, lines 23– 26). In particular, the relationship of Caprin1 and pY-Caprin1 with the recent classification by MacAinsh et al. (ref. 72) in terms of “high net charge” and “screening” classes is now also stated, as suggested by this reviewer, on p. 18 under “Discussion” (lines 26–30).

(3) Mechanistic interpretations can be further simplified or clarified. (i) Reentrant salt effects (e.g., Fig. 4a) are reported but no simple explanation seems to have been provided. Fig. 4a,b look very similar to what has been reported as strong-attraction promotor and weak-attraction suppressor, respectively (ref. 50; see also PMC5928213 Fig. 2d,b). According to the latter two studies, the “reentrant” behavior of a strong-attraction promotor, CL- in the present case, is due to Cl-mediated attraction at low to medium [NaCl] and repulsion between Cl- ions at high salt. Do the authors agree with this explanation? If not, could they provide another simple physical explanation? (ii) The authors attributed the promotional effect of Cl- to counterionbridged interchain contacts, based on a single instance. There is another simple explanation, i.e., neutralization of the net charge on Caprin1. The authors should analyze their simulation results to distinguish net charge neutralization and interchain bridging; see MacAinsh et al.

The relationship of Cl− in bridging and neutralizing configurations, respectively, with the classification of “strong-attraction promoter” and “weak-attraction suppressor” by Zhou and coworkers is now stated on p. 13 (lines 29–31), with reference to original ref. 50 by Ghosh, Mazarakos & Zhou (now ref. 59 in the revised manuscript) as well as the earlier patchy particle model study PMC5928213 by Nguemaha & Zhou, now cited as ref. 58 in the revised manuscript. After receiving this referee report, we have conducted an extensive survey of our coarse-grained MD data to provide a quantitative description of the prevalence of counterion (Cl−) bridging interactions linking positively charged arginines (Arg+s) on different Caprin1 chains in the condensed phase (using the [Na+] = 0 case as an example). The newly compiled data is reported under a new subsection heading “Explicit-ion MD offers insights into counterion-mediated interchain bridging interactions among condensed Caprin1 molecules” on p. 12 (last five lines)–p. 14 (first 10 lines) [∼ 1_._5 additional page] as well as a new Fig. 6 to depict the statistics of various Arg+–Cl−–Arg+ configurations, with the conclusion that a vast majority (at least 87%) of Cl− counterions in the Caprin1-condensed phase engage in favorable condensation-driving interchain bridging interactions.

(4) The authors presented ATP-Mg both as a single ion and as two separate ions; there is no explanation of which of the two versions reflects reality. When presenting ATP-Mg as a single ion, it’s as though it forms a salt with Na+. I assume NaCl, ATP, and MgCl2 were used in the experiment. Why is Cl- not considered? Related to this point, it looks like ATP is just another salt ion studied and much of the Results section is on NaCl, so the emphasis of ATP (“Diverse Roles of ATP” in the title is somewhat misleading.

We model ATP and ATP-Mg both as single-bead ions (in rG-RPA) and also as structurally more realistic short multiple-bead polymers (in field-theoretic simulation, FTS). We have now added discussions to clarify our modeling rationale in using and comparing different models for ATP and ATP-Mg, as follows:

p. 8 (lines 19–36):

“The complementary nature of our multiple methodologies allows us to focus sharply on the electrostatic aspects of hydrolysis-independent role of ATP in biomolecular condensation by comparing ATP’s effects with those of simple salt. Here, Caprin1 and pY-Caprin1 are modeled minimally as heteropolymers of charged and neutral beads in rG-RPA and FTS. ATP and ATP-Mg are modeled as simple salts (singlebead ions) in rG-RPA whereas they are modeled with more structural complexity as short charged polymers (multiple-bead chains) in FTS, though the latter models are still highly coarse-grained. Despite this modeling difference, rG-RPA and FTS both rationalize experimentally observed ATP- and NaCl-modulated reentrant LLPS of Caprin1 and a lack of a similar reentrance for pY-Caprin1 as well as a prominent colocalization of ATP with the Caprin1 condensate. Consistently, the same contrasting trends in the effect of NaCl on Caprin1 and pY-Caprin1 are also seen in our coarse-grained MD simulations, though polymer field theories tend to overestimate LLPS propensity [99]. The robustness of the theoretical trends across different modeling platforms underscores electrostatics as a significant component in the diverse roles of ATP in the context of its well-documented ability to modulate biomolecular LLPS via hydrophobic and π-related effects [63, 65, 67].”

Here, the last sentence quoted above addresses this reviewer’s question about our intended meaning in referring to “diverse roles of ATP” in the title of our paper. To make this point even clearer, we have also added the following sentence to the Abstract (p. 2, lines 12–13):

“... The electrostatic nature of these features complements ATP’s involvement in π-related interactions and as an amphiphilic hydrotrope, ...”

Moreover, to enhance readability, we have now added pointers in the rG-RPA part of our paper to anticipate the structurally more complex ATP and ATP-Mg models to be introduced subsequently in the FTS part, as follows:

p. 9 (lines 13–15):

“As mentioned above, in the present rG-RPA formulation, (ATP-Mg)²⁻ and ATP⁴⁻ are modeled minimally as a single-bead ion. They are represented by charged polymer models with more structural complexity in the FTS models below.”

p. 11 (lines 8–11):

These observations from analytical theory will be corroborated by FTS below with the introduction of structurally more realistic models of (ATP-Mg) ²⁻, ATP⁴⁻ together with the possibility of simultaneous inclusion of Na⁺, Cl−, and Mg²⁺ in the FTS models of Caprin1/pY-Caprin1 LLPS systems.

Reviewer #2 (Public Review):

Summary:

In this paper, Lin and colleagues aim to understand the role of different salts on the phase behavior of a model protein of significant biological interest, Caprin1, and its phosphorylated variant, pY-Caprin1. To achieve this, the authors employed a variety of methods to complement experimental studies and obtain a molecular-level understanding of ion partitioning inside biomolecular condensates. A simple theory based on rG-RPA is shown to capture the different salt dependencies of Caprin1 and pY-Caprin1 phase separation, demonstrating excellent agreement with experimental results. The application of this theory to multivalent ions reveals many interesting features with the help of multicomponent phase diagrams. Additionally, the use of CG model-based MD simulations and FTS provides further clarity on how counterions can stabilize condensed phases.

Strengths:

The greatest strength of this study lies in the integration of various methods to obtain complementary information on thermodynamic phase diagrams and the molecular details of the phase separation process. The authors have also extended their previously proposed theoretical approaches, which should be of significant interest to other researchers. Some of the findings reported in this paper, such as bridging interactions, are likely to inspire new studies using higher-resolution atomistic MD simulations.

Weaknesses:

The paper does not have any major issues.

We are very encouraged by this reviewer’s positive assessment of our work.

Reviewer #3 (Public Review):

Authors first use rG-RPA to reproduce two observed trends. Caprin1 does not phase separate at very low salt but then undergoes LLPS with added salt while further addition of salt reduces its propensity to LLPS. On the other hand pY-Caprin1 exhibits a monotonic trend where the propensity to phase separate decreases with the addition of salt. This distinction is captured by a two component model and also when salt ions are explicitly modeled as a separate species with a ternary phase diagram. The predicted ternary diagrams (when co and counter ions are explicitly accounted for) also predict the tendency of ions to co-condense or exclude proteins in the dense phase. Predicted trends are generally in line with the measurement for Cparin1 [sic]. Next, the authors seek to explain the observed difference in phase separation when Arginines are replaced by Lysines creating different variants. In the current rG-RPA type models both Arginine (R) and Lysine (K) are treated equally since non-electrostatic effects are only modeled in a meanfield manner that can be fitted but not predicted. For this reason, coarse grain MD simulation is suitable. Moreover, MD simulation affords structural features of the condensates. They used a force field that is capable of discriminating R and K. The MD predicted degrees of LLPS of these variants again is consistent with the measurement. One additional insight emerges from MD simulations that a negative ion can form a bridge between two positively charged residues on the chain. These insights are not possible to derive from rG-RPA. Both rG-RPA and MD simulation become cumbersome when considering multiple types of ions such as Na, Cl, [ATP] and [ATP-Mg] all present at the same time. FTS is well suited to handle this complexity. FTS also provides insights into the co-localization of ions and proteins that is consistent with NMR. By using different combinations of ions they confirm the robustness of the prediction that Caprin1 shows salt-dependent reentrant behavior, adding further support that the differential behavior of Caprin1, and pY-Caprin1 is likely to be mediated by charge-charge interactions.

We are encouraged by this reviewer’s positive assessment of our manuscript.

Reviewer #1 (Recommendations For The Authors):

Analysis:

Analyze the simulation results to distinguish net charge neutralization and interchain bridging; see MacAinsh et al.

Please see response above to points (3) and (4) under “Weaknesses” in this reviewer’s public review. We have now added a 1.5-page subsection starting from the bottom of p. 12 to the top of p. 14 to discuss a new extensive analysis of Arg⁺–Cl⁻–Arg⁺ configurations to identify bridging interactions, with key results reported in a new Fig. 6 (p. 42). Recent results from MacAinsh, Dey & Zhou (cited now as ref. 72) are included in the added discussion. Relevant advances made in MacAinsh et al., including clarification and classification of salt-mediated interactions in the phase separation of A1-LCD are now mentioned multiple times in the revised manuscript (p. 5, lines 19–20; p. 6, lines 2–5; p. 11, line 30; p. 14, line 10; p. 18, lines 28–29; and p. 20, line 4).

Writing and presentation

(1) Cite subtle effects that may be missed by the coarser approaches in this study

Please see response above to point (1) under “Weaknesses” in this reviewer’s public review.

(2) Try to distill the findings into a simple set of conclusions

Please see response above to point (2) under “Weaknesses” in this reviewer’s public review.

(3) Clarify and simplify physical interpretations

Please see response above to point (2) under “Weaknesses” in this reviewer’s public review.

(4) Explain the treatment of ATP-Mg as either a single ion or two separate ions; reconsider modifying the reference to ATP in the title

Please see response above to point (4) under “Weaknesses” in this reviewer’s public review.

(5) Minor points:

p. 4, citation of ref 56: this work shows ATP is a driver of LLPS, not merely a regulator (promotor or suppressor)

This citation to original ref. 56 (now ref. 63) on p. 4 is now corrected (bottom line of p. 4).

p. 7 and throughout: “using bulk [Caprin1]” – I assume this is the initial overall Caprin1 concentration. It would avoid confusion to state such concentrations as “initial” or “initial overall”

We have now added “initial overall concentration” in parentheses on p. 8 (line 4) to clarify the meaning of “bulk concentration”.

p. 7 and throughout: both mM (also uM) and mg/ml have been used as units of protein concentration and that can cause confusion. Indeed, the authors seem to have confused themselves on p. 9, where 400 (750) mM is probably 400 (750) mg/ml. The same with the use of mM and M for salt concentrations (400 mM Mg2+ but 0.1 and 1.0 M Na+)

Concentrations are now given in both molarity and mass density in Fig. 1 (p. 37), Fig. 2 (p. 38), Fig. 4 (p. 40), and Fig. 7 (p. 43), as noted in the text on p. 8 (lines 4–5). Inconsistencies and errors in quoting concentrations are now corrected (p. 10, line 18, and p. 11, line 2).

p. 7, “LCST-like”: isn’t this more like a case of a closed coexistence curve that contains both UCST and LCST?

The discussion on p. 8 around this observation from Fig. 1d is now expanded, including alluding to the theoretical possibility of a closed co-existence curve mentioned by this reviewer, as follows:

“Interestingly, the decrease in some of the condensed-phase [pY-Caprin1]s with decreasing T (orange and green symbols for ≲ 20◦C in Fig. 1d trending toward slightly lower [pY-Caprin1]) may suggest a hydrophobicity-driven lower critical solution temperature (LCST)-like reduction of LLPS propensity as temperature approaches ∼ 0◦C as in cold denaturation of globular proteins [7,23] though the hypothetical LCST is below 0◦C and therefore not experimentally accessible. If that is the case, the LLPS region would resemble those with both an UCST and a LCST [4]. As far as simple modeling is concerned, such a feature may be captured by a FH model wherein interchain contacts are favored by entropy at intermediate to low temperatures and by enthalpy at high temperatures, thus entailing a heat capacity contribution in χ(T), with [7,109,110] beyond the temperature-independent ϵ_h and ϵ_s used in Fig. 1c,d and Fig. 2. Alternatively, a reduction in overall condensed-phase concentration can also be caused by formation of heterogeneous locally organized structures with large voids at low temperatures even when interchain interactions are purely enthalpic (Fig. 4 of ref. [111]).”

p. 8 “Caprin1 can undergo LLPS without the monovalent salt (Na+) ions (LLPS regions extend to [Na+] = 0 in Fig. 2e,f”: I don’t quite understand what’s going on here. Is the effect caused by a small amount of counterion (ATP-Mg) that’s calculated according to eq 1 (with z s set to 0)?

The discussion of this result in Fig. 2e,f is now clarified as follows (p. 10, lines 8–14 in the revised manuscript):

“The corresponding rG-RPA results (Fig. 2e–h) indicate that, in the present of divalent counterions (needed for overall electric neutrality of the Caprin1 solution), Caprin1 can undergo LLPS without the monvalent salt (Na+) ions (LLPS regions extend to [Na+] = 0 in Fig. 2e,f; i.e., ρs \= 0, ρc > 0 in Eq. (1)), because the configurational entropic cost of concentrating counterions in the Caprin1 condensed phase is lesser for divalent (zc \= 2) than for monovalent (zc \= 1) counterions as only half of the former are needed for approximate electric neutrality in the condensed phase.”

p. 9 “Despite the tendency for polymer field theories to overestimate LLPS propensity and condensed-phase concentrations”: these limitations should be mentioned earlier, along with the very high concentrations (e.g., 1200 mg/ml) in Fig. 2

This sentence (now on p. 11, lines 11–18) is now modified to clarify the intended meaning as suggested by this reviewer:

“Despite the tendency for polymer field theories to overestimate LLPS propensity and condensed-phase concentrations quantitatively because they do not account for ion condensation [99]—which can be severe for small ions with more than ±1 charge valencies as in the case of condensed [Caprin1] ≳ 120 mM in Fig. 2i–l, our present rG-RPA-predicted semi-quantitative trends are consistent with experiments indicating “

In addition, this limitation of polymer field theories is also mentioned earlier in the text on p. 6, lines 30–31.

Reviewer #2 (Recommendations For The Authors):

(1) he current version of the paper goes through many different methodologies, but how these methods complement or overlap in terms of their applicability to the problem at hand may not be so clear. This can be especially difficult for readers not well-versed in these methods. I suggest the authors summarize this somewhere in the paper.

As mentioned above in response to Reviewer #1, we have now added a subsection with heading “Overview of key observations from complementary approaches” at the beginning of the “Results” section on p. 6 (lines 18–37) and the first line of p. 7 to make our paper more accessible to readers who might not be well-versed in the various theoretical and computational techniques. A few sentences to summarize our key results are added as well to the first paragraph of “Discussion” (p. 18, lines 23–26).

(2) It wasn’t clear if the authors obtained LCST-type behavior in Figure 1d or if another phenomenon is responsible for the non-monotonic change in dense phase concentrations. At the very least, the authors should comment on the possibility of observing LCST behavior using the rG-RPA model and if modifications are needed to make the theory more appropriate for capturing LCST.

As mentioned above in response to Reviewer #1, the discussion regarding possible LCSTtype behanvior in Fig. 1d is now expanded to include two possible physical origins: (i) hydrophobicity-like temperature-dependent effective interactions, and (ii) formation of heterogeneous, more open structures in the condensed phase at low temperatures. Three additional references [109, 110, 111] (from the Dill, Chan, and Panagiotopoulos group respectively) are now included to support the expanded discussion. Again, the modified discussion is as follows:

“Interestingly, the decrease in some of the condensed-phase [pY-Caprin1]s with decreasing T (orange and green symbols for ≲ 20◦C in Fig. 1d trending toward slightly lower [pY-Caprin1]) may suggest a hydrophobicity-driven lower critical solution temperature (LCST)-like reduction of LLPS propensity as temperature approaches ∼ 0◦C as in cold denaturation of globular proteins [7,23] though the hypothetical LCST is below 0◦C and therefore not experimentally accessible. If that is the case, the LLPS region would resemble those with both an UCST and a LCST [4]. As far as simple modeling is concerned, such a feature may be captured by a FH model wherein interchain contacts are favored by entropy at intermediate to low temperatures and by enthalpy at high temperatures, thus entailing a heat capacity contribution in χ(T), with [7,109,110] beyond the temperature-independent ϵ_h and ϵ_s used in Fig. 1c,d and Fig. 2. Alternatively, a reduction in overall condensed-phase concentration can also be caused by formation of heterogeneous locally organized structures with large voids at low temperatures even when interchain interactions are purely enthalpic (Fig. 4 of ref. [111]).”

(3) In Figures 4c and 4d, ionic density profiles could be shown as a separate zoomed-in version to make it easier to see the results.

This is an excellent suggestion. Two such panels are now added to Fig. 4 (p. 40) as parts (g) and (h).

Reviewer #3 (Recommendations For The Authors):

I would suggest authors make some minor edits as noted here.

(1) Please note down the chi values that were used when fitting experimental phase diagrams with rG-RPA theory in Figure 2a,b. At present there aren’t too many such values available in the literature and reporting these would help to get an estimate of effective chi values when electrostatics is appropriately modeled using rG-RPA.

The χ(T) values and their enthalpic and entropic components ϵh and ϵs used to fit the experimental data in Fig. 1c,d are now stated in the caption for Fig. 1 (p. 37). Same fitted χ(T) values are used in Fig. 2 (p. 38) as it is now stated in the revised caption for Fig. 2. Please note that for clarity we have now changed the notation from ∆h and ∆s in our originally submitted manuscript to ϵh and ϵs in the revised text (p. 7, last line) as well as in the revised figure captions to conform to the notation in our previous works [18, 71].

(2) Authors note “monovalent positive salt ions such as Na+ can be attracted, somewhat counterintuitively, into biomolecular condensates scaffolded by positively-charged polyelectrolytic IDRs in the presence of divalent counterions”. This may be due to the fact that the divalent negative counterions present in the dense phase (as seen in the ternary phase diagrams) also recruit a small amount of Na+.

The reviewer’s comment is valid, as a physical explanation for this prediction is called for. Accordingly, the following sentence is added to p. 10, lines 27–29:

“This phenomenon arises because the positively charge monovalent salt ions are attracted to the negatively charged divalent counterions in the protein-condensed phase.”

(3) In the discussion where authors contrast the LLPS propensity of Caprin1 against FUS, TDP43, Brd4, etc, they correctly note majority of these other proteins have low net charge and possibly higher non-electrostatic interaction that can promote LLPS at room temperature even in the absence of salt. It is also worth noting if some of these proteins were forced to undergo LLPS with crowding which is sometimes typical. A quick literature search will make this clear.

A careful reading of the work in question (Krainer et al., ref. 50) does not suggest that crowders were used to promote LLPS for the proteins the authors studied. Nonetheless, the reviewer’s point regarding the potential importance of crowder effects is well taken. Accordingly, crowder effects are now mentioned briefly in the Introduction (p. 4, line 13), with three additional references on the impact of crowding on LLPS added [30–32] (from the Spruijt, Mukherjee, and Rakshit groups respectively). In this connection, to provide a broader historical context to the introductory discussion of electrostatics effects in biomolecular processes in general, two additional influential reviews (from the Honig and Zhou groups respectively) are now cited as well [15, 16].

Author response:

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

Reviewer 1:

(1) Peptides were synthesized with fluorescein isothiocyanate (FITC) and Tat tag, and then PEGylated with methoxy PEG Succinimidyl Succinate.

I have two concerns about the peptide design. First, FTIC was intended "for monitoring" (line 129), but was never used in the manuscript. Second, PEGylation targets the two lysine sidechains on the Tat, which would alter its penetration property.

We conducted an analysis of the cellular trafficking of FITC-tagged peptides following their permeabilization into cells.

Author response image 1.

However, we did not include it in the main text because it is a basic result.

(2) As can be seen in the figure above, after pegylation and permeabilization, the cells were stained with FITC. It appears that this does not affect the ability to penetrate into the cells.

(2) "Superdex 200 increase 10/300 GL column" (line 437) was used to isolate mono/di PEGylated PDZ and separate them from the residual PEG and PDZ peptide. "m-PEG-succinimidyl succinate with an average molecular weight of 5000 Da" (lines 133 and 134).

To my knowledge, the Superdex 200 increase 10/300 GL column is not suitable and is unlikely to produce traces shown in Figure 1B.

As Superdex 200 increase 10/300 GL featrues a fractionation range of 10,000 to 600,000 Da, we used it to fractionate PEGylated products including DiPEGylated PDZ (approx. 15 kDa) and MonoPEGylated PDZ (approx. 10 kDa) from residuals (PDZ and PEG), demonstrating successful isolation of PEGylated products (Figure 1C). Considering the molecular weights of PDZ and PEG are approximately 4.1 kDa and and 5.0 kDa, respectively, the late eluting peaks from SEC were likely to represent a mixed absorbance of PDZ and PEG at 215 nm.

However, as the reviewer pointed out, it could be unreasonable to annotate peaks representing PDZ and PEG, respectively, from mixed absorbance detected in a region (11-12 min) beyond the fractionation range.

In our revised manuscript, therefore, multiple peaks in the late eluting volume (11-12 min) were labeled as 'Residuals' all together. As a reference, the revised figure 1B includes a chromatogram of pure PDZ-WT under the same analytic condition.

Therefore, we changed Fig.1B to new results as followed:

(3) "the in vivo survival effect of LPS and PDZ co-administration was examined in mice. The pretreatment with WT PDZ peptide significantly increased survival and rescued compared to LPS only; these effects were not observed with the mut PDZ peptide (Figure 2a)." (lines 159-160).

Fig 2a is the weight curve only. The data is missing in the manuscript.

We added the survived curve into Fig. 2A as followed:

(4) Table 1, peptide treatment on ALT and AST appears minor.

In mice treated with LPS, levels of ALT and AGT in the blood are elevated, but these levels decrease upon treatment with WT PDZ. However, the use of mut PDZ does not result in significant changes. Figure 3A shows inflammatory cells within the central vein, yet no substantial hepatotoxicity is observed during the 5-day treatment with LPS. Normally, the ranges of ALT and AGT in C57BL6 mice are 16 ~ 200 U/L and 46 ~ 221 U/L, respectively, according to UCLA Diagnostic Labs. Therefore, the values in all experiments fall within these normal ranges. In summary, a 5-day treatment with LPS induces inflammation in the liver but is too short a duration to induce hepatotoxicity, resulting in lower values.

(5) MitoTraker Green FM shouldn't produce red images in Figure 6.

We changed new results (GREEN one) into Figs 6A and B as followed:

(6) Figure 5. Comparison of mRNA expression in PDZ-treated BEAS-2B cells. Needs a clearer and more detailed description both in the main text and figure legend. The current version is very hard to read.

We changed Fig. 5A to new one to understand much easier and added more detailed results and figure legend as followed:

Results Section in Figure 5:

“…we performed RNA sequencing analysis. The results of RNA-seq analysis showed the expression pattern of 24,424 genes according to each comparison combination, of which the results showed the similarity of 51 genes overlapping in 4 gene categories and the similarity between each comparison combination (Figure 5a). As a result, compared to the control group, it was confirmed that LPS alone, WT PDZ+LPS, and mut PDZ+LPS were all upregulated above the average value in each gene, and when LPS treatment alone was compared with WT PDZ+LPS, it was confirmed that they were averaged or downregulated. When comparing LPS treatment alone and mut PDZ+LPS, it was confirmed that about half of the genes were upregulated. Regarding the similarity between comparison combinations, the comparison combination with LPS…”

Figure 5 Legend Section:

“Figure 5. Comparison of mRNA expression in PDZ-treated BEAS-2B cells.

BEAS-2B cells were treated with wild-type PDZ or mutant PDZ peptide for 24 h and then incubated with LPS for 2 h, after which RNA sequencing analysis was performed. (a) The heat map shows the general regulation pattern of about 51 inflammation-related genes that are differentially expressed when WT PDZ and mut PDZ are treated with LPS, an inflammatory substance. All samples are RED = upregulated and BLUE = downregulated relative to the gene average. Each row represents a gene, and the columns represent the values of the control group treated only with LPS and the WT PDZ and mut PDZ groups with LPS. This was used by converting each log value into a fold change value. All genes were adjusted to have the same mean and standard deviation, the unit of change is the standard deviation from the mean, and the color value range of each row is the same. (b) Significant genes were selected using Gene category chat (Fold change value of 2.00 and normalized data (log2) value of 4.00). The above pie chart shows the distribution of four gene categories when comparing LPS versus control, WT PDZ+LPS/LPS, and mut PDZ+LPS/LPS. The bar graph below shows RED=upregulated, GREEN=downregulated for each gene category, and shows the number of upregulated and downregulated genes in each gene category. (c) The protein-protein interaction network constructed by the STRING database differentially displays commonly occurring genes by comparing WT PDZ+LPS/LPS, mut PDZ+LPS/LPS, and LPS. These nodes represent proteins associated with inflammation, and these connecting lines denote interactions between two proteins. Different line thicknesses indicate types of evidence used in predicting the associations.”

Reviewer 2:

(1) In this paper, the authors demonstrated the anti-inflammatory effect of PDZ peptide by inhibition of NF-kB signaling. Are there any results on the PDZ peptide-binding proteins (directly or indirectly) that can regulate LPS-induced inflammatory signaling pathway? Elucidation of the PDZ peptide-its binding partner protein and regulatory mechanisms will strengthen the author's hypothesis about the anti-inflammatory effects of PDZ peptide

As mentioned in the Discussion section, we believe it is crucial to identify proteins that directly interact with PDZ and regulate it. This direct interaction can modulate intracellular signaling pathways, so we plan to express GST-PDZ and induce binding with cellular lysates, then characterize it using the LC-Mass/Mass method. We intend to further research these findings and submit them for publication.

(2) The authors presented interesting insights into the therapeutic role of the PDZ motif peptide of ZO-1. PDZ domains are protein-protein interaction modules found in a variety of species. It has been thought that many cellular and biological functions, especially those involving signal transduction complexes, are affected by PDZ-mediated interactions. What is the rationale for selecting the core sequence that regulates inflammation among the PDZ motifs of ZO-1 shown in Figure 1A?

The rationale for selecting the core sequence that regulates inflammation among the PDZ motifs of ZO-1, as shown in Figure 1A, is grounded in the specific roles these motifs play in signal transduction pathways that are crucial for inflammatory processes. PDZ domains are recognized for their ability to function as scaffolding proteins that organize signal transduction complexes, crucial for modulating cellular and biological functions. The chosen core sequence is particularly important because it is conserved across ZO-1, ZO-2, and ZO-3, indicating a fundamental role in maintaining cellular integrity and signaling pathways. This conservation suggests that the sequence’s involvement in inflammatory regulation is not only significant in ZO-1 but also reflects a broader biological function across the ZO family.

(3) In Figure 3, the authors showed the representative images of IHC, please add the quantification analysis of Iba1 expression and PAS-positive cells using Image J or other software. To help understand the figure, an indication is needed to distinguish specifically stained cells (for example, a dotted line or an arrow).

We added the semi-quantitative results into Figs. 4d,e,f as followed:

Result section: “The specific physiological mechanism by which WT PDZ peptide decreases LPS-induced systemic inflammation in mice and the signal molecules involved remain unclear. These were confirmed by a semi-quantitative analysis of Iba-1 immunoreactivity and PAS staining in liver, kidney, and lung,respectively (Figures 4d, e, and f). To examine whether WT PDZ peptide can alter LPS-induced tissue damage in the kidney, cell toxicity assay was performed (Figure 3g). LPS induced cell damage in the kidney, however, WT PDZ peptide could significantly alleviate the toxicity, but mut PDZ peptide could not. Because cytotoxicity caused by LPS is frequently due to ROS production in the kidney (Su et al., 2023; Qiongyue et al., 2022), ROS production in the mitochondria was investigated in renal mitochondria cells harvested from kidney tissue (Figure 3h)....”

Figure legend section: “Indicated scale bars were 20 μm. (d,e,f) Semi-quantitative analysis of each are positive for Iba-1 in liver and kidney, and positive cells of PAS in lung, respectively. (g) After the kidneys were harvested, tissue lysates were used for MTT assay. (h) After...”

(4) In Figure 6G, H, the authors confirmed the change in expression of the M2 markers by PDZ peptide using the mouse monocyte cell line Raw264.7. It would be good to add an experiment on changes in M1 and M2 markers caused by PDZ peptides in human monocyte cells (for example, THP-1).

We thank you for your comments. To determine whether PDZ peptide regulates M1/M2 polarization in human monocytes, we examined changes in M1 and M2 gene expression in THP-1 cells. As a result, wild-type PDZ significantly suppressed the expression of M1 marker genes (hlL-1β, hIL-6, hIL-8, hTNF-ɑ), while increasing the expression of M2 marker genes (hlL-4, hIL-10, hMRC-1). However, mutant PDZ did not affect M1/M2 polarization. These results suggest that PDZ peptide can suppress inflammation by regulating M1/M2 polarization of human monocyte cells. These results are for the reviewer's reference only and will not be included in the main content.

Author response image 2.

Author response image 3.

Minor point:

The use of language is appropriate, with good writing skills. Nevertheless, a thorough proofread would eliminate small mistakes such as:

- line 254, " mut PDZ+LPS/LPS (45.75%) " → " mut PDZ+LPS/LPS (47.75%) "

- line 296, " Figure 6f " → " Figure 6h "

We changed these points into the manuscript.

Author response:

eLife Assessment

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

We thank the Reviewing editor and Senior editor at eLife for their positive assessment of our paper. After reading the reviewers’ comments – to which we reply below - we agree that the presentation of the data could be completed. We provide additional presentation of data in the responses below and we will slightly modify Figure 2 of the paper. However, in keeping the short format of the paper, the revised version will have the same number of figures, which support the claims made in the paper.

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

We thank reviewer #1 for their positive evaluation of our paper. Obviously, we agree with the reviewer that the paper would be much stronger if BOTH effects – spike increase and decrease – would be found in BOTH patients in their corresponding fMRI regions (lateral and medial fusiform gyrus) (also in the same hemisphere). Nevertheless, we clearly acknowledge this limitation in the (revised) version of the manuscript (p.8: Material and Methods section).

In the current paper, one could think that P1 shows only increases to faces, and P2 would show only decreases (irrespective of the region). However, that is not the case since 11% of P1’s face-selective units are decreases (89% are increases) and 4% of P2’s face-selective units are increases. This has now been made clearer in the manuscript (p.5).

As the reviewer is certainly aware, the number and position of the electrodes are based on strict clinical criteria, and we will probably never encounter a situation with two neighboring (macro-micro hybrid electrodes), one with microelectrodes ending up in the lateral MidFG, the other in the medial MidFG, in the same patient. If there is no clinical value for the patient, this cannot be done.

The only thing we can do is to strengthen these results in the future by collecting data on additional patients with an electrode either in the lateral or the medial FG, together with fMRI. But these are the only two patients we have been able to record so far with electrodes falling unambiguously in such contrasted regions and with large (and comparable) measures.

While we acknowledge that the results may be unique because of the use of 2 contrasted patients only (and this is why the paper is a short report), the data is compelling in these 2 cases, and we are confident that it will be replicated in larger cohorts in the future.

Reviewer #2 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

The authors claim that the results tell us about both 1) face-selectivity in the fusiform gyrus, and 2) the physiological basis of the BOLD signal. However, I would like to see more of the data that supports the first claim, and I am not sure the second claim is supported.

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

We thank reviewer #2 for their positive evaluation of our paper. We understand the reviewer’s point, and we partly agree. Where we respectfully disagree is that the finding of absolute suppression is critical for the claim of the paper: finding an identical contrast between the two regions in terms of RELATIVE increase/decrease of face-selective activity in fMRI and spiking activity is already novel and informative. Where we agree with the reviewer is that the absolute suppression could be more documented: it wasn’t, due to space constraints (brief report). We provide below an example of a neuron showing absolute suppression to faces. In the frequency domain, there is only a face-selective response (1.2 Hz and harmonics) but no significant response at 6 Hz (common general visual response). In the time-domain, relative to face onset, the response drops below baseline level. It means that this neuron has baseline (non-periodic) spontaneous spiking activity that is actively suppressed when a face appears.

Author response image 1.

(2) I am not sure how much light the results shed on the physiological basis of the BOLD signal. The authors write that the results reveal "that BOLD decreases can be due to relative, but also absolute, spike suppression in the human brain" (line 120). But I think to make this claim, you would need a region that exclusively had neurons showing absolute suppression, not a region with a mix of neurons, some showing absolute suppression and some showing relative suppression, as here. The responses of both groups of neurons contribute to the measured BOLD signal, so it seems impossible to tell from these data how absolute suppression per se drives the BOLD response.

It is a fact that we find both kinds of responses in the same region.  We cannot tell with this technique if neurons showing relative vs. absolute suppression of responses are spatially segregated for instance (e.g., forming two separate sub-regions) or are intermingled. And we cannot tell from our data how absolute suppression per se drives the BOLD response. In our view, this does not diminish the interest and originality of the study, but the statement "that BOLD decreases can be due to relative, but also absolute, spike suppression in the human brain” will be rephrased in the revised manuscript, in the following way: "that BOLD decreases can be due to relative, or absolute (or a combination of both), spike suppression in the human brain”.

Reviewer #3 (Public review):

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

Strengths:

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

Weaknesses:

My major concerns are two-fold:

(i) There is a paucity of data; Thus, more information (results and methods) is warranted; and in particular there is no comparison between the fMRI data and the SEEG data.

We thank reviewer #3 for their positive evaluation of our paper. If the reviewer means paucity of data presentation, we agree and we provide more presentation below, although the methods and results information appear as complete to us. The comparison between fMRI and SEEG is there, but can only be indirect (i.e., collected at different times and not related on a trial-by-trial basis for instance). In addition, our manuscript aims at providing a short empirical contribution to further our understanding of the relationship between neural responses and BOLD signal, not to provide a model of neurovascular coupling.

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

We understand the concern of the reviewer, but we respectfully disagree that our paradigm cannot distinguish between lower firing rate to faces vs. suppression of response to faces. Indeed, since the stimuli are presented periodically (6 Hz), we can objectively distinguish stimulus-related activity from spontaneous neuronal firing. The baseline corresponds to spikes that are non-periodic, i.e., unrelated to the (common face and object) stimulation. For a subset of neurons, even this non-periodic baseline activity is suppressed, above and beyond the suppression of the 6 Hz response illustrated on Figure 2. We mention it in the manuscript, but we agree that we do not present illustrations of such decrease in the time-domain for SU, which we did not consider as being necessary initially (please see below for such presentation).

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

We answer to more specific requests for additional evidence below, but the reviewer should be aware that this is a short report, which reaches the word limit. In our view, the group average neural data should be sufficient to support the conclusions, and the example neurons are there for illustration. And while we cannot provide the raster plots for a large number of neurons, the anonymized data will be made available upon publication of the final version of the paper.

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

As mentioned above the comparison between fMRI and SEEG is indirect (i.e., collected at different times and not related on a trial-by-trial basis for instance) and would not allow to make such a model.

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

The data has been analyzed comprehensively, but we would not be able to show all neurons with such significant visual responses and face-selective responses.

(c) The neuron shown in E shows cyclical responses tied to the onset of the stimuli, is this the visual response?

Correct, it’s the visual response at 6 Hz.

If so, why is there an increase in the firing rate of the neuron before the face stimulus is shown in time 0?

Because the stimulation is continuous. What is displayed at 0 is the onset of the face stimulus, with each face stimulus being preceded by 4 images of nonface objects.

The neuron's data seems different than the average response across neurons; This raises a concern about interpreting the average response across neurons in panel F which seems different than the single neuron responses

The reviewer is correct, and we apologize for the confusion. This is because the average data on panel F has been notch-filtered for the 6 Hz (and harmonic responses), as indicated in the methods (p.11):  ‘a FFT notch filter (filter width = 0.05 Hz) was then applied on the 70 s single or multi-units time-series to remove the general visual response at 6 Hz and two additional harmonics (i.e., 12 and 18 Hz)’.

Here is the same data without the notch-filter (the 6Hz periodic response is clearly visible):

Author response image 2.

For sake of clarity, we prefer presenting the notch-filtered data in the paper, but the revised version will make it clear in the figure caption that the average data has been notch-filtered.

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

We agree with the reviewer that this is interesting, but again we do not think that it is necessary for the point made in the present paper. Responses in these regions appear rather heterogenous, and we are currently working on a longer paper with additional SEEG data (other patients tested for shorter sessions) to define and quantify the face-selective neurons in the MidFusiform gyrus with this approach (without relating it to the fMRI contrast as reported here).

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

We agree with the reviewer and have modified Figure 2 accordingly in the revised manuscript.

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

The fast periodic paradigm to measure neural face-selectivity has been used in tens of studies since its original reports:

- in EEG: Rossion et al., 2015: https://doi.org/10.1167/15.1.18

- in SEEG: Jonas et al., 2016: https://doi.org/10.1073/pnas.1522033113

In this paradigm, the face-selective response spreads to several harmonics (1.2 Hz, 2.4 Hz, 3.6 Hz, etc.) (which are summed for quantifying the total face-selective amplitude). This is illustrated below by the averaged single units’ SNR spectra across all recording sessions for both participants.

Author response image 3.

There is no unique phase-value, each harmonic being associated with a phase-value, so that the timing cannot be unambiguously extracted from phase values. Instead, the onset latency is computed directly from the time-domain responses, which is more straightforward and reliable than using the phase. Note that the present paper is not about the specific time-courses of the different types of neurons, which would require a more comprehensive report, but which is not necessary to support the point made in the present paper about the SEEG-fMRI sign relationship.

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

Face-selectivity is defined as a DIFFERENTIAL response to faces compared to objects, not necessarily a larger response to faces. So yes, face-selectivity in P1 is an increase in response to faces and P2 a reduction in response to faces.

(1) Additional methods

(a) it is unclear if the SSVEP analyses of neural responses were done on the spikes or the raw electrical signal. If the former, how is the SSVEP frequency analysis done on discrete data like action potentials?

The FFT is applied directly on spike trains using Matlab’s discrete Fourier Transform function. This function is suitable to be applied to spike trains in the same way as to any sampled digital signal (here, the microwires signal was sampled at 30 kHz, see Methods).

In complementary analyses, we also attempted to apply the FFT on spike trains that had been temporally smoothed by convolving them with a 20ms square window (Le Cam et al., 2023, cited in the paper ). This did not change the outcome of the frequency analyses in the frequency range we are interested in.

(b) it is unclear why the onset time was shifted by 33ms; one can measure the phase of the response relative to the cycle onset and use that to estimate the delay between the onset of a stimulus and the onset of the response. Adding phase information will be useful.

The onset time was shifted by 33ms because the stimuli are presented with a sinewave contrast modulation (i.e., at 0ms, the stimulus has 0% contrast). 100% contrast is reached at half a stimulation cycle, which is 83.33ms here, but a response is likely triggered before reaching 100% contrast. To estimate the delay between the start of the sinewave (0% contrast) and the triggering of a neural response, we tested 7 SEEG participants with the same images presented in FPVS sequences either as a sinewave contrast (black line) modulation or as a squarewave (i.e. abrupt) contrast modulation (red line).  The 33ms value is based on these LFP data obtained in response to such sinewave stimulation and squarewave stimulation of the same paradigm. This delay corresponds to 4 screen refresh frames (120 Hz refresh rate = 8.33ms by frame) and 35% of the full contrast, as illustrated below (please see also Retter, T. L., & Rossion, B. (2016). Uncovering the neural magnitude and spatio-temporal dynamics of natural image categorization in a fast visual stream. Neuropsychologia, 91, 9–28).

Author response image 4.

(2) Interpretation of suppression:

The SSVEP paradigm alternates between 2 conditions: faces and objects and has no baseline; In other words, responses to faces are measured relative to the baseline response to objects so that any region that contains neurons that have a lower firing rate to faces than objects is bound to show a lower response in the SSVEP signal. Therefore, because the experiment does not have a true baseline (e.g. blank screen, with no visual stimulation) this experimental design cannot distinguish between lower firing rate to faces vs suppression of response to faces.

The strongest evidence put forward for suppression is the response of non-visual neurons that was also reduced when patients looked at faces, but since these are non-visual neurons, it is unclear how to interpret the responses to faces.

We understand this point, but how does the reviewer know that these are non-visual neurons? Because these neurons are located in the visual cortex, they are likely to be visual neurons that are not responsive to non-face objects. In any case, as the reviewer writes, we think it’s strong evidence for suppression.

We thank all three reviewers for their positive evaluation of our paper and their constructive comments.

Author Response

Reviewer 1:

Comment 1.1: The distinction of PIGS from nearby OPA, which has also been implied in navigation and ego-motion, is not as clear as it could be.

Response1.1: The main functional distinction between TOS/OPA and PIGS is that TOS/OPA responds preferentially to moving vs. stationary stimuli (even concentric rings), likely due to its overlap with the retinotopic motion-selective visual area V3A, for which this is a defining functional property (e.g. Tootell et al., 1997, J Neurosci). In comparison, PIGS does not show such a motion-selectivity. Instead, PIGS responds preferentially to more complex forms of motion within scenes. In this revision, we tried to better highlight this point in the Discussion (see also the response to the first comment from Reviewer #2).

Reviewer 2:

Comment 2.1: First, the scene-selective region identified appears to overlap with regions that have previously been identified in terms of their retinotopic properties. In particular, it is unclear whether this region overlaps with V7/IPS0 and/or IPS1. This is particularly important since prior work has shown that OPA often overlaps with v7/IPS0 (Silson et al, 2016, Journal of Vision). The findings would be much stronger if the authors could show how the location of PIGS relates to retinotopic areas (other than V6, which they do currently consider). I wonder if the authors have retinotopic mapping data for any of the participants included in this study. If not, the authors could always show atlas-based definitions of these areas (e.g. Wang et al, 2015, Cerebral Cortex).

Response 2.1: We thank the reviewers for reminding us to more clearly delineate this issue of possible overlap, including the information provided by Silson et al, 2016. The issue of possible overlap between area TOS/OPA and the retinotopic visual areas, both in humans and non-human primates, was also clarified by our team in 2011 (Nasr et al., 2011). As you can see in the enclosed figure, and consistent with those previous studies, TOS/OPA overlaps with visual areas V3A/B and V7. Whereas PIGS is located more dorsally close to IPS2-4. As shown here, there is no overlap between PIGS and TOS/OPA and there is no overlap between PIGS and areas V3A/B and V7. To more directly address the reviewer’s concern, in the next revision, we will show the relative position of PIGS and the retinotopic areas (at least) in one individual subject.

Author response image 1.

The relative location of PIGS, TOS/OPA and the retinotopic visual areas. The left panel showed the result of high-resolution (7T; voxel size = 1 mm; no spatial smoothing) polar angle mapping in one individual. The right panel shows the location of scene-selective areas PIGS and TOS/OPA in the same subject (7T; voxel size = 1 mm; no spatial smoothing). While area TOS/OPA shows some overlap with the retinotopic visual areas V3A/B and V7, PIGS shows partial overlap with area IPS2-4. In both panels, the activity maps are overlaid on the subjects’ own reconstructed brain surface.

Comment 2.2: Second, recent studies have reported a region anterior to OPA that seems to be involved in scene memory (Steel et al, 2021, Nature Communications; Steel et al, 2023, The Journal of Neuroscience; Steel et al, 2023, biorXiv). Is this region distinct from PIGS? Based on the figures in those papers, the scene memory-related region is inferior to V7/IPS0, so characterizing the location of PIGS to V7/IPS0 as suggested above would be very helpful here as well. If PIGS overlaps with either of V7/IPS0 or the scene memory-related area described by Steel and colleagues, then arguably it is not a newly defined region (although the characterization provided here still provides new information).

Response 2.2: The lateral-place memory area (LPMA) is located on the lateral brain surface, anterior relative to the IPS (see Figure 1 from Steel et al., 2021 and Figure 3 from Steel et al., 2023). In contrast, PIGS is located on the posterior brain surface, also posterior relative to the IPS. In other words, they are located on two different sides of a major brain sulcus. In this revision we have clarified this point, including the citations by Steel and colleagues.

Comments 2.3: Another reason that it would be helpful to relate PIGS to this scene memory area is that this scene memory area has been shown to have activity related to the amount of visuospatial context (Steel et al, 2023, The Journal of Neuroscience). The conditions used to show the sensitivity of PIGS to ego-motion also differ in the visuospatial context that can be accessed from the stimuli. Even if PIGS appears distinct from the scene memory area, the degree of visuospatial context is an alternative account of what might be represented in PIGS.

Response 2.3: The reviewer raises an interesting point. One minor confusion is that we may be inadvertently referring to two slightly different types of “visuospatial context”. Specifically, the stimuli used in the ego-motion experiment here (i.e. coherently vs. incoherently changing scenes) represent the same scenes, and the only difference between the two conditions is the sequence of images across the experimental blocks. In that sense, the two experimental conditions may be considered to have the same visuospatial context. However, it could be also argued that the coherently changing scenes provide more information about the environmental layout. In that case, considering the previous reports that PPA/TPA and RSC/MPA may also be involved in layout encoding (Epstein and Kanwisher 1998; Wolbers et al. 2011), we expected to see more activity within those regions in response to coherently compared incoherently changing scenes. These issues are now more explicitly discussed in the revised article.

Reviewer 3:

Comment 3.1: There are few weaknesses in this work. If pressed, I might say that the stimuli depicting ego-motion do not, strictly speaking, depict motion, but only apparent motion between 2s apart photographs. However, this choice was made to equate frame rates and motion contrast between the 'ego-motion' and a control condition, which is a useful and valid approach to the problem. Some choices for visualization of the results might be made differently; for example, outlines of the regions might be shown in more plots for easier comparison of activation locations, but this is a minor issue.

Response 3.1: We thank the reviewer for these constructive suggestions, and we agree with their comment that the ego-motion stimuli are not smooth, even though they were refreshed every 100 ms. However, the stimuli were nevertheless coherent enough to activate areas V6 and MT, two major areas known to respond preferentially to coherent compared to incoherent motion.

Epstein, R., and N. Kanwisher. 1998. 'A cortical representation of the local visual environment', Nature, 392: 598-601.

Wolbers, T., R. L. Klatzky, J. M. Loomis, M. G. Wutte, and N. A. Giudice. 2011. 'Modality-independent coding of spatial layout in the human brain', Curr Biol, 21: 984-9.

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Author response:

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

Reviewer #1 (Public review): 

The authors present a substantial improvement to their existing tool, MorphoNet, intended to facilitate assessment of 3D+t cell segmentation and tracking results, and curation of high-quality analysis for scientific discovery and data sharing. These tools are provided through a user-friendly GUI, making them accessible to biologists who are not experienced coders. Further, the authors have re-developed this tool to be a locally installed piece of software instead of a web interface, making the analysis and rendering of large 3D+t datasets more computationally efficient. The authors evidence the value of this tool with a series of use cases, in which they apply different features of the software to existing datasets and show the improvement to the segmentation and tracking achieved. 

While the computational tools packaged in this software are familiar to readers (e.g., cellpose), the novel contribution of this work is the focus on error correction. The MorphoNet 2.0 software helps users identify where their candidate segmentation and/or tracking may be incorrect. The authors then provide existing tools in a single user-friendly package, lowering the threshold of skill required for users to get maximal value from these existing tools. To help users apply these tools effectively, the authors introduce a number of unsupervised quality metrics that can be applied to a segmentation candidate to identify masks and regions where the segmentation results are noticeably different from the majority of the image. 

This work is valuable to researchers who are working with cell microscopy data that requires high-quality segmentation and tracking, particularly if their data are 3D time-lapse and thus challenging to segment and assess. The MorphoNet 2.0 tool that the authors present is intended to make the iterative process of segmentation, quality assessment, and re-processing easier and more streamlined, combining commonly used tools into a single user interface.   

We sincerely thank the reviewer for their thorough and encouraging evaluation of our work. We are grateful that they highlighted both the technical improvements of MorphoNet 2.0 and its potential impact for the broader community working with complex 3D+t microscopy datasets. We particularly appreciate the recognition of our efforts to make advanced segmentation and tracking tools accessible to non-expert users through a user-friendly and locally installable interface, and for pointing out the importance of error detection and correction in the iterative analysis workflow. The reviewer’s appreciation of the value of integrating unsupervised quality metrics to support this process is especially meaningful to us, as this was a central motivation behind the development of MorphoNet 2.0. We hope the tool will indeed facilitate more rigorous and reproducible analyses, and we are encouraged by the reviewer’s positive assessment of its utility for the community.

One of the key contributions of the work is the unsupervised metrics that MorphoNet 2.0 offers for segmentation quality assessment. These metrics are used in the use cases to identify low-quality instances of segmentation in the provided datasets, so that they can be improved with plugins directly in MorphoNet 2.0. However, not enough consideration is given to demonstrating that optimizing these metrics leads to an improvement in segmentation quality. For example, in Use Case 1, the authors report their metrics of interest (Intensity offset, Intensity border variation, and Nuclei volume) for the uncurated silver truth, the partially curated and fully curated datasets, but this does not evidence an improvement in the results. Additional plotting of the distribution of these metrics on the Gold Truth data could help confirm that the distribution of these metrics now better matches the expected distribution. 

Similarly, in Use Case 2, visual inspection leads us to believe that the segmentation generated by the Cellpose + Deli pipeline (shown in Figure 4d) is an improvement, but a direct comparison of agreement between segmented masks and masks in the published data (where the segmentations overlap) would further evidence this. 

We agree that demonstrating the correlation between metric optimization and real segmentation improvement is essential. We have added new analysis comparing the distributions of the unsupervised metrics with the gold truth data before and after curation. Additionally, we provided overlap scores where ground truth annotations are available, confirming the improvement. We also explicitly discussed the limitation of relying solely on unsupervised metrics without complementary validation.

We would appreciate the authors addressing the risk of decreasing the quality of the segmentations by applying circular logic with their tool; MorphoNet 2.0 uses unsupervised metrics to identify masks that do not fit the typical distribution. A model such as StarDist can be trained on the "good" masks to generate more masks that match the most common type. This leads to a more homogeneous segmentation quality, without consideration for whether these metrics actually optimize the segmentation 

We thank the reviewer for this important and insightful comment. It raises a crucial point regarding the risk of circular logic in our segmentation pipeline. Indeed, relying on unsupervised metrics to select “good” masks and using them to train a model like StarDist could lead to reinforcing a particular distribution of shapes or sizes, potentially filtering out biologically relevant variability. This homogenization may improve consistency with the chosen metrics, but not necessarily with the true underlying structures.

We fully agree that this is a key limitation to be aware of. We have revised the manuscript to explicitly discuss this risk, emphasizing that while our approach may help improve segmentation quality according to specific criteria, it should be complemented with biological validation and, when possible, expert input to ensure that important but rare phenotypes are not excluded.

In Use case 5, the authors include details that the errors were corrected by "264 MorphoNet plugin actions ... in 8 hours actions [sic]". The work would benefit from explaining whether this is 8 hours of human work, trying plugins and iteratively improving, or 8 hours of compute time to apply the selected plugins. 

We clarified that the “8 hours” refer to human interaction time, including exploration, testing, and iterative correction using plugins. 

Reviewer #2 (Public review):

Summary: 

This article presents Morphonet 2.0, a software designed to visualise and curate segmentations of 3D and 3D+t data. The authors demonstrate their capabilities on five published datasets, showcasing how even small segmentation errors can be automatically detected, easily assessed, and corrected by the user. This allows for more reliable ground truths, which will in turn be very much valuable for analysis and training deep learning models. Morphonet 2.0 offers intuitive 3D inspection and functionalities accessible to a non-coding audience, thereby broadening its impact. 

Strengths: 

The work proposed in this article is expected to be of great interest to the community by enabling easy visualisation and correction of complex 3D(+t) datasets. Moreover, the article is clear and well written, making MorphoNet more likely to be used. The goals are clearly defined, addressing an undeniable need in the bioimage analysis community. The authors use a diverse range of datasets, successfully demonstrating the versatility of the software. 

We would also like to highlight the great effort that was made to clearly explain which type of computer configurations are necessary to run the different datasets and how to find the appropriate documentation according to your needs. The authors clearly carefully thought about these two important problems and came up with very satisfactory solutions. 

We would like to sincerely thank the reviewer for their positive and thoughtful feedback. We are especially grateful that they acknowledged the clarity of the manuscript and the potential value of MorphoNet 2.0 for the community, particularly in facilitating the visualization and correction of complex 3D(+t) datasets. We also appreciate the reviewer’s recognition of our efforts to provide detailed guidance on hardware requirements and access to documentation—two aspects we consider crucial to ensuring the tool is both usable and widely adopted. Their comments are very encouraging and reinforce our commitment to making MorphoNet 2.0 as accessible and practical as possible for a broad range of users in the bioimage analysis community.

Weaknesses: 

There is still one concern: the quantification of the improvement of the segmentations in the use cases and, therefore, the quantification of the potential impact of the software. While it appears hard to quantify the quality of the correction, the proposed work would be significantly improved if such metrics could be provided. 

The authors show some distributions of metrics before and after segmentations to highlight the changes. This is a great start, but there seem to be two shortcomings: first, the comparison and interpretation of the different distributions does not appear to be trivial. It is therefore difficult to judge the quality of the improvement from these. Maybe an explanation in the text of how to interpret the differences between the distributions could help. A second shortcoming is that the before/after metrics displayed are the metrics used to guide the correction, so, by design, the scores will improve, but does that accurately represent the improvement of the segmentation? It seems to be the case, but it would be nice to maybe have a better assessment of the improvement of the quality. 

We thank the reviewer for this constructive and important comment. We fully agreed that assessing the true quality improvement of segmentation after correction is a central and challenging issue. While we initially focused on changes in the unsupervised quality metrics to illustrate the effect of the correction, we acknowledged that interpreting these distributions was not always straightforward, and that relying solely on the metrics used to guide the correction introduced an inherent bias in the evaluation.

To address the first point, we revised the manuscript to provide clearer guidance on how to interpret the changes in metric distributions before and after correction, with additional examples to make this interpretation more intuitive.

Regarding the second point, we agreed that using independent, external validation was necessary to confirm that the segmentation had genuinely improved. To this end, we included additional assessments using complementary evaluation strategies on selected datasets where ground truth was accessible, to compare pre- and post-correction segmentations with an independent reference. These results reinforced the idea that the corrections guided by unsupervised metrics generally led to more accurate segmentations, but we also emphasized their limitations and the need for biological validation in real-world cases.

Reviewer #3 (Public review): 

Summary: 

A very thorough technical report of a new standalone, open-source software for microscopy image processing and analysis (MorphoNet 2.0), with a particular emphasis on automated segmentation and its curation to obtain accurate results even with very complex 3D stacks, including timelapse experiments. 

Strengths: 

The authors did a good job of explaining the advantages of MorphoNet 2.0, as compared to its previous web-based version and to other software with similar capabilities. What I particularly found more useful to actually envisage these claimed advantages is the five examples used to illustrate the power of the software (based on a combination of

Python scripting and the 3D game engine Unity). These examples, from published research, are very varied in both types of information and image quality, and all have their complexities, making them inherently difficult to segment. I strongly recommend the readers to carefully watch the accompanying videos, which show (although not thoroughly) how the software is actually used in these examples. 

We sincerely thanked the reviewer for their thoughtful and encouraging feedback. We were particularly pleased that the reviewer appreciated the comparative analysis of MorphoNet 2.0 with both its earlier version and existing tools, as well as the relevance of the five diverse and complex use cases we had selected. Demonstrating the software’s versatility and robustness across a variety of challenging datasets was a key goal of this work, and we were glad that this aspect came through clearly. We also appreciated the reviewer’s recommendation to watch the accompanying videos, which we had designed to provide a practical sense of how the tool was used in real-world scenarios. Their positive assessment was highly motivating and reinforced the value of combining scripting flexibility with an interactive 3D interface.

Weaknesses: 

Being a technical article, the only possible comments are on how methods are presented, which is generally adequate, as mentioned above. In this regard, and in spite of the presented examples (chosen by the authors, who clearly gave them a deep thought before showing them), the only way in which the presented software will prove valuable is through its use by as many researchers as possible. This is not a weakness per se, of course, but just what is usual in this sort of report. Hence, I encourage readers to download the software and give it time to test it on their own data (which I will also do myself).   

We fully agreed that the true value of MorphoNet 2.0 would be demonstrated through its practical use by a wide range of researchers working with complex 3D and 3D+t datasets. In this regard, we improved the user documentation and provided a set of example datasets to help new users quickly familiarize themselves with the platform. We were also committed to maintaining and updating MorphoNet 2.0 based on user feedback to further support its usability and impact.

In conclusion, I believe that this report is fundamental because it will be the major way of initially promoting the use of MorphoNet 2.0 by the objective public. The software itself holds the promise of being very impactful for the microscopists' community. 

Reviewer #1 (Recommendations for the authors): 

(1) In Use Case 1, when referring to Figure 3a, they describe features of 3b? 

We corrected the mismatch between Figure 3a and 3b descriptions.

(2) In Figure 3g-I, columns for Curated Nuclei and All Nuclei appear to be incorrectly labelled, and should be the other way around. 

We corrected  the label swapped between “Curated Nuclei” and “All Nuclei.”

(3) Some mention of how this will be supported in the future would be of interest. 

We added a note on long-term support plans  

(4) Could Morphonet be rolled into something like napari and integrated into its environment with access to its plugins and tools? 

We thank the reviewer for this pertinent suggestion. We fully recognize the growing importance of interoperability within the bioimage analysis community, and we have been working on establishing a bridge between MorphoNet and napari to enable data exchange and complementary use of the two tools. As a platform, all new developments are first evaluated by our beta testers before being officially released to the user community and subsequently documented. The interoperability component is still under active development and will be announced shortly in a beta-testing phase. For this reason, we were not able to include it in the present manuscript, but we plan to document it in a future release.

(5) Can meshes be extracted/saved in another format? 

We agreed that the ability to extract and save meshes in standard formats was highly useful for interoperability with other tools. We implemented this feature in the new version of MorphoNet, allowing users to export meshes in commonly used formats such as OBJ or STL. Response: We thank the reviewer for this pertinent suggestion. We fully recognize the growing importance of interoperability within the bioimage analysis community, and we have been working on establishing a bridge between MorphoNet and napari to enable data exchange and complementary use of the two tools. As a platform, all new developments are first evaluated by our beta testers before being officially released to the user community and subsequently documented. The interoperability component is still under active development and will be announced shortly in a beta-testing phase. For this reason, we were not able to include it in the present manuscript, but we plan to document it in a future release.

Reviewer #2 (Recommendations for the authors): 

As a comment, since the authors mentioned the recent progress in 3D segmentation of various biological components, including organelles, it could be interesting to have examples of Morphonet applied to investigate subcellular structures. These present different challenges in visualization and quantification due to their smaller scale.

We thank the reviewer for this insightful suggestion. We fully agree that applying MorphoNet 2.0 to the analysis of sub-cellular structures is a promising direction, particularly given the specific challenges these datasets present in terms of resolution, visualization, and quantification. While our current use cases focus on cellular and tissue-level segmentation, we are actively interested in extending the applicability of the tool to finer scales. We are currently exploring plugins for spot detection and curation in single-molecule FISH data. However, this requires more time to properly validate relevant use cases, and we plan to include this functionality in the next release.

Another comment is that the authors briefly mention two other state-of-the-art softwares (namely FIJI and napari) but do not really position MorphoNet against them. The text would likely benefit from such a comparison so the users can better decide which one to use or not. 

We agreed that providing a clearer comparison between MorphoNet 2.0 and other widely used tools such as FIJI and Napari would greatly benefit readers and potential users. In response, we included a new paragraph in the supplementary materials of the revised manuscript, highlighting the main features, strengths, and limitations of each tool in the context of 3D+t segmentation, visualization, and correction workflows. This addition helped users better understand the positioning of MorphoNet 2.0 and make informed choices based on their specific needs.

Minor comments: 

L 439: The Deli plugin is mentioned but not introduced in the main text; it could be helpful to have an idea of what it is without having to dive into the supplementary material. 

We included a brief description in the main text and thoroughly revise the help pages to improve clarity

Figure 4: It is not clear how the potential holes created by the removal of objects are handled. Are the empty areas filled by neighboring cells, for example, are they left empty? 

We clarified in the figure legend of Figure 4.

Please remove from the supplementary the use cases that are already in the main text. 

We cleaned up redundant use case descriptions.

Typos: 

L 22: the end of the sentence is missing. 

L 51: There are two "."   

L 370: replace 'et' with 'and'.   

L 407-408, Figure 3: panels g-i, the columns 'curated nuclei' and 'all nuclei' seem to be inverted. 

L 549: "four 4". 

Reviewer #3 (Recommendations for the authors): 

Dear Authors, what follows are "minor comments" (the only sort of comment I have for this nice report): 

Minor issues: 

(1) Not being a user of MorphoNet, I found that reading the manuscript was a bit hard due to the several names of plugins or tools that are mentioned, many times without a clear explanation of what they do. One way of improving this could be to add a table, a sort of glossary, with those names, a brief explanation of what they are, and a link to their "help" page on the web. 

We understood that the manuscript might be difficult to follow for readers unfamiliar with MorphoNet, especially due to the numerous plugin and tool names referenced. To address this, we carried out a complete overhaul of the help pages to make them clearer, more structured, and easier to navigate.

(2) Figure 4d, orthogonal view: It is claimed that this segmentation is correct according to the original intensity image, but it is not clear why some cells in the border actually appear a lot bigger than other cells in the embryo. It does look like an incomplete segmentation due to the poor image quality at the border. Whether this is the case or if the authors consider the contrary, it should be somehow explained/discussed in the figure legend or the main text. 

We revised the figure legend and main text to acknowledge the challenge of segmenting peripheral regions with low signal-to-noise ratios and discussed how this affects segmentation.

Small writing issues I could spot:   

Line 247: there is a double point after "Sup. Mat..". 

Line 329: probably a diagrammation error of the pdf I use to review, there is a loose sentence apparently related to a figure: "Vegetal view ofwith smoothness". 

Line 393 (and many other places): avoid using numbers when it is not a parameter you are talking about, and the number is smaller than 10. In this case, it should be: "The five steps...". 

Line 459: Is "opposite" referring to "Vegetal", like in g? In addition, it starts with lower lowercase. 

Lines 540-541: Check if redaction is correct in "...projected the values onto the meshed dual of the object..." (it sounds obscure to me). 

Lines 548-549: Same thing for "...included two groups of four 4 nuclei and one group of 3 fused nuclei.". 

Line 637: Should it be "Same view as b"? 

Line 646: "The property highlights..."? 

Line 651: In the text, I have seen a "propagation plugin" named as "Prope", "Propa", and now "Propi". Are they all different? Is it a mistake? Please, see my first "Minor issue", which might help readers navigate through this sort of confusing nomenclature. 

Line 702: I personally find the use of the term "eco-system" inappropriate in this context. We scientists know what an ecosystem is, and the fact that it has now become a fashionable word for politicians does not make it correct in any context. 

We thank the reviewer for their careful reading of the manuscript and for pointing out these writing and typographic issues. We corrected all the mentioned points in the revised version, including punctuation, sentence clarity, consistent naming of tools (e.g., the propagation plugin), and appropriate use of terms such as “ecosystem.” We also appreciated the suggestion to avoid numerals for numbers under ten when not referring to parameters, and we ensured consistency throughout the text. These corrections improved the clarity and readability of the manuscript, and we were grateful for the reviewer’s attention to detail.

Author response:

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

Reviewer #1 (Public Review):

Lu & Golomb combined EEG, artificial neural networks, and multivariate pattern analyses to examine how different visual variables are processed in the brain. The conclusions of the paper are mostly well supported, but some aspects of methods and data analysis would benefit from clarification and potential extensions.

The authors find that not only real-world size is represented in the brain (which was known), but both retinal size and real-world depth are represented, at different time points or latencies, which may reflect different stages of processing. Prior work has not been able to answer the question of real-world depth due to the stimuli used. The authors made this possible by assessing real-world depth and testing it with appropriate methodology, accounting for retinal and real-world size. The methodological approach combining behavior, RSA, and ANNs is creative and well thought out to appropriately assess the research questions, and the findings may be very compelling if backed up with some clarifications and further analyses.

The work will be of interest to experimental and computational vision scientists, as well as the broader computational cognitive neuroscience community as the methodology is of interest and the code is or will be made available. The work is important as it is currently not clear what the correspondence between many deep neural network models and the brain is, and this work pushes our knowledge forward on this front. Furthermore, the availability of methods and data will be useful for the scientific community.

Reviewer #2 (Public Review):

Summary:

This paper aims to test if neural representations of images of objects in the human brain contain a 'pure' dimension of real-world size that is independent of retinal size or perceived depth. To this end, they apply representational similarity analysis on EEG responses in 10 human subjects to a set of 200 images from a publicly available database (THINGS-EEG2), correlating pairwise distinctions in evoked activity between images with pairwise differences in human ratings of real-world size (from THINGS+). By partialling out correlations with metrics of retinal size and perceived depth from the resulting EEG correlation time courses, the paper claims to identify an independent representation of real-world size starting at 170 ms in the EEG signal. Further comparisons with artificial neural networks and language embeddings lead the authors to claim this correlation reflects a relatively 'high-level' and 'stable' neural representation.

Strengths:

The paper features insightful figures/illustrations and clear figures.

The limitations of prior work motivating the current study are clearly explained and seem reasonable (although the rationale for why using 'ecological' stimuli with backgrounds matters when studying real-world size could be made clearer; one could also argue the opposite, that to get a 'pure' representation of the real-world size of an 'object concept', one should actually show objects in isolation).

The partial correlation analysis convincingly demonstrates how correlations between feature spaces can affect their correlations with EEG responses (and how taking into account these correlations can disentangle them better).

The RSA analysis and associated statistical methods appear solid.

Weaknesses:

The claim of methodological novelty is overblown. Comparing image metrics, behavioral measurements, and ANN activations against EEG using RSA is a commonly used approach to study neural object representations. The dataset size (200 test images from THINGS) is not particularly large, and neither is comparing pre-trained DNNs and language models, or using partial correlations.

Thanks for your feedback. We agree that the methods used in our study – such as RSA, partial correlations, and the use of pretrained ANN and language models – are indeed well-established in the literature. We therefore revised the manuscript to more carefully frame our contribution: rather than emphasizing methodological novelty in isolation, we now highlight the combination of techniques, the application to human EEG data with naturalistic images, and the explicit dissociation of real-world size, retinal size, and depth representations as the primary strengths of our approach. Corresponding language in the Abstract, Introduction, and Discussion has been adjusted to reflect this more precise positioning:

(Abstract, line 34 to 37) “our study combines human EEG and representational similarity analysis to disentangle neural representations of object real-world size from retinal size and perceived depth, leveraging recent datasets and modeling approaches to address challenges not fully resolved in previous work.”

(Introduction, line 104 to 106) “we overcome these challenges by combining human EEG recordings, naturalistic stimulus images, artificial neural networks, and computational modeling approaches including representational similarity analysis (RSA) and partial correlation analysis …”

(Introduction, line 108) “We applied our integrated computational approach to an open EEG dataset…”

(Introduction, line 142 to 143) “The integrated computational approach by cross-modal representational comparisons we take with the current study…”

(Discussion, line 550 to 552) “our study goes beyond the contributions of prior studies in several key ways, offering both theoretical and methodological advances: …”

The claims also seem too broad given the fairly small set of RDMs that are used here (3 size metrics, 4 ANN layers, 1 Word2Vec RDM): there are many aspects of object processing not studied here, so it's not correct to say this study provides a 'detailed and clear characterization of the object processing process'.

Thanks for pointing this out. We softened language in our manuscript to reflect that our findings provide a temporally resolved characterization of selected object features, rather than a comprehensive account of object processing:

(line 34 to 37) “our study combines human EEG and representational similarity analysis to disentangle neural representations of object real-world size from retinal size and perceived depth, leveraging recent datasets and modeling approaches to address challenges not fully resolved in previous work.”

(line 46 to 48) “Our research provides a temporally resolved characterization of how certain key object properties – such as object real-world size, depth, and retinal size – are represented in the brain, …”

The paper lacks an analysis demonstrating the validity of the real-world depth measure, which is here computed from the other two metrics by simply dividing them. The rationale and logic of this metric is not clearly explained. Is it intended to reflect the hypothesized egocentric distance to the object in the image if the person had in fact been 'inside' the image? How do we know this is valid? It would be helpful if the authors provided a validation of this metric.

We appreciate the comment regarding the real-world depth metric. Specifically, this metric was computed as the ratio of real-world size (obtained via behavioral ratings) to measured retinal size. The rationale behind this computation is grounded in the basic principles of perspective projection: for two objects subtending the same retinal size, the physically larger object is presumed to be farther away. This ratio thus serves as a proxy for perceived egocentric depth under the simplifying assumption of consistent viewing geometry across images.

We acknowledge that this is a derived estimate and not a direct measurement of perceived depth. While it provides a useful approximation that allows us to analytically dissociate the contributions of real-world size and depth in our RSA framework, we agree that future work would benefit from independent perceptual depth ratings to validate or refine this metric. We added more discussions about this to our revised manuscript:

(line 652 to 657) “Additionally, we acknowledge that our metric for real-world depth was derived indirectly as the ratio of perceived real-world size to retinal size. While this formulation is grounded in geometric principles of perspective projection and served the purpose of analytically dissociating depth from size in our RSA framework, it remains a proxy rather than a direct measure of perceived egocentric distance. Future work incorporating behavioral or psychophysical depth ratings would be valuable for validating and refining this metric.”

Given that there is only 1 image/concept here, the factor of real-world size may be confounded with other things, such as semantic category (e.g. buildings vs. tools). While the comparison of the real-world size metric appears to be effectively disentangled from retinal size and (the author's metric of) depth here, there are still many other object properties that are likely correlated with real-world size and therefore will confound identifying a 'pure' representation of real-world size in EEG. This could be addressed by adding more hypothesis RDMs reflecting different aspects of the images that may correlate with real-world size.

We thank the reviewer for this thoughtful and important point. We agree that semantic category and real-world size may be correlated, and that semantic structure is one of the plausible sources of variance contributing to real-world size representations. However, we would like to clarify that our original goal was to isolate real-world size from two key physical image features — retinal size and inferred real-world depth — which have been major confounds in prior work on this topic. We acknowledge that although our analysis disentangled real-world size from depth and retinal size, this does not imply a fully “pure” representation; therefore, we now refer to the real-world size representations as “partially disentangled” throughout the manuscript to reflect this nuance.

Interestingly, after controlling for these physical features, we still found a robust and statistically isolated representation of real-world size in the EEG signal. This motivated the idea that realworld size may be more than a purely perceptual or image-based property — it may be at least partially semantic. Supporting this interpretation, both the late layers of ANN models and the non-visual semantic model (Word2Vec) also captured real-world size structure. Rather than treating semantic information as an unwanted confound, we propose that semantic structure may be an inherent component of how the brain encodes real-world size.

To directly address the your concern, we conducted an additional variance partitioning analysis, in which we decomposed the variance in EEG RDMs explained by four RDMs: real-world depth, retinal size, real-world size, and semantic information (from Word2Vec). Specifically, for each EEG timepoint, we quantified (1) the unique variance of real-world size, after controlling for semantic similarity, depth, and retinal size; (2) the unique variance of semantic information, after controlling for real-world size, depth, and retinal size; (3) the shared variance jointly explained by real-world size and semantic similarity, controlling for depth and retinal size. This analysis revealed that real-world size explained unique variance in EEG even after accounting for semantic similarity. And there was also a substantial shared variance, indicating partial overlap between semantic structure and size. Semantic information also contributed unique explanatory power, as expected. These results suggest that real-world size is indeed partially semantic in nature, but also has independent neural representation not fully explained by general semantic similarity. This strengthens our conclusion that real-world size functions as a meaningful, higher-level dimension in object representation space.

We now include this new analysis and a corresponding figure (Figure S8) in the revised manuscript:

(line 532 to 539) “Second, we conducted a variance partitioning analysis, in which we decomposed the variance in EEG RDMs explained by three hypothesis-based RDMs and the semantic RDM (Word2Vec RDM), and we still found that real-world size explained unique variance in EEG even after accounting for semantic similarity (Figure S9). And we also observed a substantial shared variance jointly explained by real-world size and semantic similarity and a unique variance of semantic information. These results suggest that real-world size is indeed partially semantic in nature, but also has independent neural representation not fully explained by general semantic similarity.”

The choice of ANNs lacks a clear motivation. Why these two particular networks? Why pick only 2 somewhat arbitrary layers? If the goal is to identify more semantic representations using CLIP, the comparison between CLIP and vision-only ResNet should be done with models trained on the same training datasets (to exclude the effect of training dataset size & quality; cf Wang et al., 2023). This is necessary to substantiate the claims on page 19 which attributed the differences between models in terms of their EEG correlations to one of them being a 'visual model' vs. 'visual-semantic model'.

We argee that the choice and comparison of models should be better contextualized.

First, our motivation for selecting ResNet-50 and CLIP ResNet-50 was not to make a definitive comparison between model classes, but rather to include two widely used representatives of their respective categories—one trained purely on visual information (ResNet-50 on ImageNet) and one trained with joint visual and linguistic supervision (CLIP ResNet-50 on image–text pairs). These models are both highly influential and commonly used in computational and cognitive neuroscience, allowing for relevant comparisons with existing work (line 181-187).

Second, we recognize that limiting the EEG × ANN correlation analyses to only early and late layers may be viewed as insufficiently comprehensive. To address this point, we have computed the EEG correlations with multiple layers in both ResNet and CLIP models (ResNet: ResNet.maxpool, ResNet.layer1, ResNet.layer2, ResNet.layer3, ResNet.layer4, ResNet.avgpool; CLIP: CLIP.visual.avgpool, CLIP.visual.layer1, CLIP.visual.layer2, CLIP.visual.layer3, CLIP.visual.layer4, CLIP.visual.attnpool). The results, now included in Figure S4, show a consistent trend: early layers exhibit higher similarity to early EEG time points, and deeper layers show increased similarity to later EEG stages. We chose to highlight early and late layers in the main text to simplify interpretation.

Third, we appreciate the reviewer’s point that differences in training datasets (ImageNet vs. CLIP's dataset) may confound any attribution of differences in brain alignment to the models' architectural or learning differences. We agree that the comparisons between models trained on matched datasets (e.g., vision-only vs. multimodal models trained on the same image–text corpus) would allow for more rigorous conclusions. Thus, we explicitly acknowledged this limitation in the text:

(line 443 to 445) “However, it is also possible that these differences between ResNet and CLIP reflect differences in training data scale and domain.”

The first part of the claim on page 22 based on Figure 4 'The above results reveal that realworld size emerges with later peak neural latencies and in the later layers of ANNs, regardless of image background information' is not valid since no EEG results for images without backgrounds are shown (only ANNs).

We revised the sentence to clarify that this is a hypothesis based on the ANN results, not an empirical EEG finding:

(line 491 to 495) “These results show that real-world size emerges in the later layers of ANNs regardless of image background information, and – based on our prior EEG results – although we could not test object-only images in the EEG data, we hypothesize that a similar temporal profile would be observed in the brain, even for object-only images.”

While we only had the EEG data of human subjects viewing naturalistic images, the ANN results suggest that real-world size representations may still emerge at later processing stages even in the absence of background, consistent with what we observed in EEG under with-background conditions.

The paper is likely to impact the field by showcasing how using partial correlations in RSA is useful, rather than providing conclusive evidence regarding neural representations of objects and their sizes.

Additional context important to consider when interpreting this work:

Page 20, the authors point out similarities of peak correlations between models ('Interestingly, the peaks of significant time windows for the EEG × HYP RSA also correspond with the peaks of the EEG × ANN RSA timecourse (Figure 3D,F)'. Although not explicitly stated, this seems to imply that they infer from this that the ANN-EEG correlation might be driven by their representation of the hypothesized feature spaces. However this does not follow: in EEG-image metric model comparisons it is very typical to see multiple peaks, for any type of model, this simply reflects specific time points in EEG at which visual inputs (images) yield distinctive EEG amplitudes (perhaps due to stereotypical waves of neural processing?), but one cannot infer the information being processed is the same. To investigate this, one could for example conduct variance partitioning or commonality analysis to see if there is variance at these specific timepoints that is shared by a specific combination of the hypothesis and ANN feature spaces.

Thanks for your thoughtful observation! Upon reflection, we agree that the sentence – "Interestingly, the peaks of significant time windows for the EEG × HYP RSA also correspond with the peaks of the EEG × ANN RSA timecourse" – was speculative and risked implying a causal link that our data do not warrant. As you rightly points out, observing coincident peak latencies across different models does not necessarily imply shared representational content, given the stereotypical dynamics of evoked EEG responses. And we think even variance partitioning analysis would still not suffice to infer that ANN-EEG correlations are driven specifically by hypothesized feature spaces. Accordingly, we have removed this sentence from the manuscript to avoid overinterpretation. 

Page 22 mentions 'The significant time-window (90-300ms) of similarity between Word2Vec RDM and EEG RDMs (Figure 5B) contained the significant time-window of EEG x real-world size representational similarity (Figure 3B)'. This is not particularly meaningful given that the Word2Vec correlation is significant for the entire EEG epoch (from the time-point of the signal 'arriving' in visual cortex around ~90 ms) and is thus much less temporally specific than the realworld size EEG correlation. Again a stronger test of whether Word2Vec indeed captures neural representations of real-world size could be to identify EEG time-points at which there are unique Word2Vec correlations that are not explained by either ResNet or CLIP, and see if those timepoints share variance with the real-world size hypothesized RDM.

We appreciate your insightful comment. Upon reflection, we agree that the sentence – "'The significant time-window (90-300ms) of similarity between Word2Vec RDM and EEG RDMs (Figure 5B) contained the significant time-window of EEG x real-world size representational similarity (Figure 3B)" – was speculative. And we have removed this sentence from the manuscript to avoid overinterpretation. 

Additionally, we conducted two analyses as you suggested in the supplement. First, we calculated the partial correlation between EEG RDMs and the Word2Vec RDM while controlling for four ANN RDMs (ResNet early/late and CLIP early/late) (Figure S8). Even after regressing out these ANN-derived features, we observed significant correlations between Word2Vec and EEG RDMs in the 100–190 ms and 250–300 ms time windows. This result suggests that

Word2Vec captures semantic structure in the neural signal that is not accounted for by ResNet or CLIP. Second, we conducted an additional variance partitioning analysis, in which we decomposed the variance in EEG RDMs explained by four RDMs: real-world depth, retinal size, real-world size, and semantic information (from Word2Vec) (Figure S9). And we found significant shared variance between Word2Vec and real-world size at 130–150 ms and 180–250 ms. These results indicate a partially overlapping representational structure between semantic content and real-world size in the brain.

We also added these in our revised manuscript:

(line 525 to 539) “To further probe the relationship between real-world size and semantic information, and to examine whether Word2Vec captures variances in EEG signals beyond that explained by visual models, we conducted two additional analyses. First, we performed a partial correlation between EEG RDMs and the Word2Vec RDM, while regressing out four ANN RDMs (early and late layers of both ResNet and CLIP) (Figure S8). We found that semantic similarity remained significantly correlated with EEG signals across sustained time windows (100-190ms and 250-300ms), indicating that Word2Vec captures neural variance not fully explained by visual or visual-language models. Second, we conducted a variance partitioning analysis, in which we decomposed the variance in EEG RDMs explained by three hypothesis-based RDMs and the semantic RDM (Word2Vec RDM), and we still found that real-world size explained unique variance in EEG even after accounting for semantic similarity (Figure S9). And we also observed a substantial shared variance jointly explained by realworld size and semantic similarity and a unique variance of semantic information. These results suggest that real-world size is indeed partially semantic in nature, but also has independent neural representation not fully explained by general semantic similarity.”

Reviewer #3 (Public Review):

The authors used an open EEG dataset of observers viewing real-world objects. Each object had a real-world size value (from human rankings), a retinal size value (measured from each image), and a scene depth value (inferred from the above). The authors combined the EEG and object measurements with extant, pre-trained models (a deep convolutional neural network, a multimodal ANN, and Word2vec) to assess the time course of processing object size (retinal and real-world) and depth. They found that depth was processed first, followed by retinal size, and then real-world size. The depth time course roughly corresponded to the visual ANNs, while the real-world size time course roughly corresponded to the more semantic models.

The time course result for the three object attributes is very clear and a novel contribution to the literature. However, the motivations for the ANNs could be better developed, the manuscript could better link to existing theories and literature, and the ANN analysis could be modernized. I have some suggestions for improving specific methods.

(1) Manuscript motivations

The authors motivate the paper in several places by asking " whether biological and artificial systems represent object real-world size". This seems odd for a couple of reasons. Firstly, the brain must represent real-world size somehow, given that we can reason about this question. Second, given the large behavioral and fMRI literature on the topic, combined with the growing ANN literature, this seems like a foregone conclusion and undermines the novelty of this contribution.

Thanks for your helpful comment. We agree that asking whether the brain represents real-world size is not a novel question, given the existing behavioral and neuroimaging evidence supporting this. Our intended focus was not on the existence of real-world size representations per se, but the nature of these representations, particularly the relationship between the temporal dynamics and potential mechanisms of representations of real-world size versus other related perceptual properties (e.g., retinal size and real-world depth). We revised the relevant sentence to better reflect our focue, shifting from a binary framing (“whether or not size is represented”) to a more mechanistic and time-resolved inquiry (“how and when such representations emerge”):

(line 144 to 149) “Unraveling the internal representations of object size and depth features in both human brains and ANNs enables us to investigate how distinct spatial properties—retinal size, realworld depth, and real-world size—are encoded across systems, and to uncover the representational mechanisms and temporal dynamics through which real-world size emerges as a potentially higherlevel, semantically grounded feature.”

While the introduction further promises to "also investigate possible mechanisms of object realworld size representations.", I was left wishing for more in this department. The authors report correlations between neural activity and object attributes, as well as between neural activity and ANNs. It would be nice to link the results to theories of object processing (e.g., a feedforward sweep, such as DiCarlo and colleagues have suggested, versus a reverse hierarchy, such as suggested by Hochstein, among others). What is semantic about real-world size, and where might this information come from? (Although you may have to expand beyond the posterior electrodes to do this analysis).

We thank the reviewer for this insightful comment. We agree that understanding the mechanisms underlying real-world size representations is a critical question. While our current study does not directly test specific theoretical frameworks such as the feedforward sweep model or the reverse hierarchy theory, our results do offer several relevant insights: The temporal dynamics revealed by EEG—where real-world size emerges later than retinal size and depth—suggest that such representations likely arise beyond early visual feedforward stages, potentially involving higherlevel semantic processing. This interpretation is further supported by the fact that real-world size is strongly captured by late layers of ANNs and by a purely semantic model (Word2Vec), suggesting its dependence on learned conceptual knowledge.

While we acknowledge that our analyses were limited to posterior electrodes and thus cannot directly localize the cortical sources of these effects, we view this work as a first step toward bridging low-level perceptual features and higher-level semantic representations. We hope future work combining broader spatial sampling (e.g., anterior EEG sensors or source localization) and multimodal recordings (e.g., MEG, fMRI) can build on these findings to directly test competing models of object processing and representation hierarchy.

We also added these to the Discussion section:

(line 619 to 638) “Although our study does not directly test specific models of visual object processing, the observed temporal dynamics provide important constraints for theoretical interpretations. In particular, we find that real-world size representations emerge significantly later than low-level visual features such as retinal size and depth. This temporal profile is difficult to reconcile with a purely feedforward account of visual processing (e.g., DiCarlo et al., 2012), which posits that object properties are rapidly computed in a sequential hierarchy of increasingly complex visual features. Instead, our results are more consistent with frameworks that emphasize recurrent or top-down processing, such as the reverse hierarchy theory (Hochstein & Ahissar, 2002), which suggests that high-level conceptual information may emerge later and involve feedback to earlier visual areas. This interpretation is further supported by representational similarities with late-stage artificial neural network layers and with a semantic word embedding model (Word2Vec), both of which reflect learned, abstract knowledge rather than low-level visual features. Taken together, these findings suggest that real-world size is not merely a perceptual attribute, but one that draws on conceptual or semantic-level representations acquired through experience. While our EEG analyses focused on posterior electrodes and thus cannot definitively localize cortical sources, we see this study as a step toward linking low-level visual input with higher-level semantic knowledge. Future work incorporating broader spatial coverage (e.g., anterior sensors), source localization, or complementary modalities such as MEG and fMRI will be critical to adjudicate between alternative models of object representation and to more precisely trace the origin and flow of real-world size information in the brain.”

Finally, several places in the manuscript tout the "novel computational approach". This seems odd because the computational framework and pipeline have been the most common approach in cognitive computational neuroscience in the past 5-10 years.

We have revised relevant statements throughout the manuscript to avoid overstating novelty and to better reflect the contribution of our study.

(2) Suggestion: modernize the approach

I was surprised that the computational models used in this manuscript were all 8-10 years old. Specifically, because there are now deep nets that more explicitly model the human brain (e.g., Cornet) as well as more sophisticated models of semantics (e.g., LLMs), I was left hoping that the authors had used more state-of-the-art models in the work. Moreover, the use of a single dCNN, a single multi-modal model, and a single word embedding model makes it difficult to generalize about visual, multimodal, and semantic features in general.

Thanks for your suggestion. Indeed, our choice of ResNet and CLIP was motivated by their widespread use in the cognitive and computational neuroscience area. These models have served as standard benchmarks in many studies exploring correspondence between ANNs and human brain activity. To address you concern, we have now added additional results from the more biologically inspired model, CORnet, in the supplementary (Figure S10). The results for CORnet show similar patterns to those observed for ResNet and CLIP, providing converging evidence across models.

Regarding semantic modeling, we intentionally chose Word2Vec rather than large language models (LLMs), because our goal was to examine concept-level, context-free semantic representations. Word2Vec remains the most widely adopted approach for obtaining noncontextualized embeddings that reflect core conceptual similarity, as opposed to the contextdependent embeddings produced by LLMs, which are less directly suited for capturing stable concept-level structure across stimuli.

(3) Methodological considerations

(a) Validity of the real-world size measurement

I was concerned about a few aspects of the real-world size rankings. First, I am trying to understand why the scale goes from 100-519. This seems very arbitrary; please clarify. Second, are we to assume that this scale is linear? Is this appropriate when real-world object size is best expressed on a log scale? Third, the authors provide "sand" as an example of the smallest realworld object. This is tricky because sand is more "stuff" than "thing", so I imagine it leaves observers wondering whether the experimenter intends a grain of sand or a sandy scene region. What is the variability in real-world size ratings? Might the variability also provide additional insights in this experiment?

We now clarify the origin, scaling, and interpretation of the real-world size values obtained from the THINGS+ dataset.

In their experiment, participants first rated the size of a single object concept (word shown on the screen) by clicking on a continuous slider of 520 units, which was anchored by nine familiar real-world reference objects (e.g., “grain of sand,” “microwave oven,” “aircraft carrier”) that spanned the full expected size range on a logarithmic scale. Importantly, participants were not shown any numerical values on the scale—they were guided purely by the semantic meaning and relative size of the anchor objects. After the initial response, the scale zoomed in around the selected region (covering 160 units of the 520-point scale) and presented finer anchor points between the previous reference objects. Participants then refined their rating by dragging from the lower to upper end of the typical size range for that object. If the object was standardized in size (e.g., “soccer ball”), a single click sufficed. These size judgments were collected across at least 50 participants per object, and final scores were derived from the central tendency of these responses. Although the final size values numerically range from 0 to 519 (after scaling), this range is not known to participants and is only applied post hoc to construct the size RDMs.

Regarding the term “sand”: the THINGS+ dataset distinguished between object meanings when ambiguity was present. For “sand,” participants were instructed to treat it as “a grain of sand”— consistent with the intended meaning of a discrete, minimal-size reference object. 

Finally, we acknowledge that real-world size ratings may carry some degree of variability across individuals. However, the dataset includes ratings from 2010 participants across 1854 object concepts, with each object receiving at least 50 independent ratings. Given this large and diverse sample, the mean size estimates are expected to be stable and robust across subjects. While we did not include variability metrics in our main analysis, we believe the aggregated ratings provide a reliable estimate of perceived real-world size.

We added these details in the Materials and Method section:

(line 219 to 230) “In the THINGS+ dataset, 2010 participants (different from the subjects in THINGS EEG2) did an online size rating task and completed a total of 13024 trials corresponding to 1854 object concepts using a two-step procedure. In their experiment, first, each object was rated on a 520unit continuous slider anchored by familiar reference objects (e.g., “grain of sand,” “microwave oven,” “aircraft carrier”) representing a logarithmic size range. Participants were not shown numerical values but used semantic anchors as guides. In the second step, the scale zoomed in around the selected region to allow for finer-grained refinement of the size judgment. Final size values were derived from aggregated behavioral data and rescaled to a range of 0–519 for consistency across objects, with the actual mean ratings across subjects ranging from 100.03 (‘grain of sand’) to 423.09 (‘subway’).”

(b) This work has no noise ceiling to establish how strong the model fits are, relative to the intrinsic noise of the data. I strongly suggest that these are included.

We have now computed noise ceiling estimates for the EEG RDMs across time. The noise ceiling was calculated by correlating each participant’s EEG RDM with the average EEG RDM across the remaining participants (leave-one-subject-out), at each time point. This provides an upper-bound estimate of the explainable variance, reflecting the maximum similarity that any model—no matter how complex—could potentially achieve, given the intrinsic variability in the EEG data.

Importantly, the observed EEG–model similarity values are substantially below this upper bound. This outcome is fully expected: Each of our model RDMs (e.g., real-world size, ANN layers) captures only a specific aspect of the neural representational structure, rather than attempting to account for the totality of the EEG signal. Our goal is not to optimize model performance or maximize fit, but to probe which components of object information are reflected in the spatiotemporal dynamics of the brain’s responses.

For clarity and accessibility of the main findings, we present the noise ceiling time courses separately in the supplementary materials (Figure S7). Including them directly in the EEG × HYP or EEG × ANN plots would conflate distinct interpretive goals: the model RDMs are hypothesis-driven probes of specific representational content, whereas the noise ceiling offers a normative upper bound for total explainable variance. Keeping these separate ensures each visualization remains focused and interpretable. 

Reviewer #1 (Recommendations For The Authors)::

Some analyses are incomplete, which would be improved if the authors showed analyses with other layers of the networks and various additional partial correlation analyses.

Clarity

(1) Partial correlations methods incomplete - it is not clear what is being partialled out in each analysis. It is possible to guess sometimes, but it is not entirely clear for each analysis. This is important as it is difficult to assess if the partial correlations are sensible/correct in each case. Also, the Figure 1 caption is short and unclear.

For example, ANN-EEG partial correlations - "Finally, we directly compared the timepoint-bytimepoint EEG neural RDMs and the ANN RDMs (Figure 3F). The early layer representations of both ResNet and CLIP were significantly correlated with early representations in the human brain" What is being partialled out? Figure 3F says partial correlation

We apologize for the confusion. We made several key clarifications and corrections in the revised version.

First, we identified and corrected a labeling error in both Figure 1 and Figure 3F. Specifically, our EEG × ANN analysis used Spearman correlation, not partial correlation as mistakenly indicated in the original figure label and text. We conducted parital correlations for EEG × HYP and ANN × HYP. But for EEG × ANN, we directly calculated the correlation between EEG RDMs and ANN RDM corresponding to different layers respectively. We corrected these errors: (1) In Figure 1, we removed the erroneous “partial” label from the EEG × ANN path and updated the caption to clearly outline which comparisons used partial correlation. (2) In Figure 3F, we corrected the Y-axis label to “(correlation)”.

Second, to improve clarity, we have now revised the Materials and Methods section to explicitly describe what is partialled out in each parital correlation analysis:

(line 284 to 286) “In EEG × HYP partial correlation (Figure 3D), we correlated EEG RDMs with one hypothesis-based RDM (e.g., real-world size), while controlling for the other two (retinal size and real-world depth).”

(line 303 to 305) “In ANN (or W2V) × HYP partial correlation (Figure 3E and Figure 5A), we correlated ANN (or W2V) RDMs with one hypothesis-based RDM (e.g., real-world size), while partialling out the other two.”

Finally, the caption of Figure 1 has been expanded to clarify the full analysis pipeline and explicitly specify the partial correlation or correlation in each comparison.

(line 327 to 332) “Figure 1 Overview of our analysis pipeline including constructing three types of RDMs and conducting comparisons between them. We computed RDMs from three sources: neural data (EEG), hypothesized object features (real-world size, retinal size, and real-world depth), and artificial models (ResNet, CLIP, and Word2Vec). Then we conducted cross-modal representational similarity analyses between: EEG × HYP (partial correlation, controlling for other two HYP features), ANN (or W2V) × HYP (partial correlation, controlling for other two HYP features), and EEG × ANN (correlation).”

We believe these revisions now make all analytic comparisons and correlation types full clear and interpretable.

Issues / open questions

(2) Semantic representations vs hypothesized (hyp) RDMs (real-world size, etc) - are the representations explained by variables in hyp RDMs or are there semantic representations over and above these? E.g., For ANN correlation with the brain, you could partial out hyp RDMs - and assess whether there is still semantic information left over, or is the variance explained by the hyp RDMs?

Thank for this suggestion. As you suggested, we conducted the partial correlation analysis between EEG RDMs and ANN RDMs, controlling for the three hypothesis-based RDMs. The results (Figure S6) revealed that the EEG×ANN representational similarity remained largely unchanged, indicating that ANN representations capture much more additional representational structure not accounted for by the current hypothesized features. This is also consistent with the observation that EEG×HYP partial correlations were themselves small, but EEG×ANN correlations were much greater.

We also added this statement to the main text:

(line 446 to 451) “To contextualize how much of the shared variance between EEG and ANN representations is driven by the specific visual object features we tested above, we conducted a partial correlation analysis between EEG RDMs and ANN RDMs controlling for the three hypothesis-based RDMs (Figure S6). The EEG×ANN similarity results remained largely unchanged, suggesting that ANN representations capture much more additional rich representational structure beyond these features. ”

(3) Why only early and late layers? I can see how it's clearer to present the EEG results. However, the many layers in these networks are an opportunity - we can see how simple/complex linear/non-linear the transformation is over layers in these models. It would be very interesting and informative to see if the correlations do in fact linearly increase from early to later layers, or if the story is a bit more complex. If not in the main text, then at least in the supplement.

Thank you for the thoughtful suggestion. To address this point, we have computed the EEG correlations with multiple layers in both ResNet and CLIP models (ResNet: ResNet.maxpool, ResNet.layer1, ResNet.layer2, ResNet.layer3, ResNet.layer4, ResNet.avgpool; CLIP:CLIP.visual.avgpool, CLIP.visual.layer1, CLIP.visual.layer2, CLIP.visual.layer3, CLIP.visual.layer4, CLIP.visual.attnpool). The results, now included in Figure S4 and S5, show a consistent trend: early layers exhibit higher similarity to early EEG time points, and deeper layers show increased similarity to later EEG stages. We chose to highlight early and late layers in the main text to simplify interpretation, but now provide the full layerwise profile for completeness.

(4) Peak latency analysis - Estimating peaks per ppt is presumably noisy, so it seems important to show how reliable this is. One option is to find the bootstrapped mean latencies per subject.

Thanks for your suggestion. To estimate the robustness of peak latency values, we implemented a bootstrap procedure by resampling the pairwise entries of the EEG RDM with replacement. For each bootstrap sample, we computed a new EEG RDM and recalculated the partial correlation time course with the hypothesis RDMs. We then extracted the peak latency within the predefined significant time window. Repeating this process 1000 times allowed us to get the bootstrapped mean latencies per subject as the more stable peak latency result. Notably, the bootstrapped results showed minimal deviation from the original latency estimates, confirming the robustness of our findings. Accordingly, we updated the Figure 3D and added these in the Materials and Methods section:

(line 289 to 298) “To assess the stability of peak latency estimates for each subject, we performed a bootstrap procedure across stimulus pairs. At each time point, the EEG RDM was vectorized by extracting the lower triangle (excluding the diagonal), resulting in 19,900 unique pairwise values. For each bootstrap sample, we resampled these 19,900 pairwise entries with replacement to generate a new pseudo-RDM of the same size. We then computed the partial correlation between the EEG pseudo-RDM and a given hypothesis RDM (e.g., real-world size), controlling for other feature RDMs, and obtained a time course of partial correlations. Repeating this procedure 1000 times and extracting the peak latency within the significant time window yielded a distribution of bootstrapped latencies, from which we got the bootstrapped mean latencies per subject.”

(5) "Due to our calculations being at the object level, if there were more than one of the same objects in an image, we cropped the most complete one to get a more accurate retinal size. " Did EEG experimenters make sure everyone sat the same distance from the screen? and remain the same distance? This would also affect real-world depth measures.

Yes, the EEG dataset we used (THINGS EEG2; Gifford et al., 2022) was collected under carefully controlled experimental conditions. We have confirmed that all participants were seated at a fixed distance of 0.6 meters from the screen throughout the experiment. We also added this information in the method (line 156 to 157).

Minor issues/questions - note that these are not raised in the Public Review

(6) Title - less about rigor/quality of the work but I feel like the title could be improved/extended. The work tells us not only about real object size, but also retinal size and depth. In fact, isn't the most novel part of this the real-world depth aspect? Furthermore, it feels like the current title restricts its relevance and impact... Also doesn't touch on the temporal aspect, or processing stages, which is also very interesting. There may be something better, but simply adding something like"...disentangled features of real-world size, depth, and retinal size over time OR processing stages".

Thanks for your suggestion! We changed our title – “Human EEG and artificial neural networks reveal disentangled representations and processing timelines of object real-world size and depth in natural images”.

(7) "Each subject viewed 16740 images of objects on a natural background for 1854 object concepts from the THINGS dataset (Hebart et al., 2019). For the current study, we used the 'test' dataset portion, which includes 16000 trials per subject corresponding to 200 images." Why test images? Worth explaining.

We chose to use the “test set” of the THINGS EEG2 dataset for the following two reasons:

(1) Higher trial count per condition: In the test set, each of the 200 object images was presented 80 times per subject, whereas in the training set, each image was shown only 4 times. This much higher trial count per condition in the test set allows for substantially higher signal-tonoise ratio in the EEG data.

(2) Improved decoding reliability: Our analysis relies on constructing EEG RDMs based on pairwise decoding accuracy using linear SVM classifiers. Reliable decoding estimates require a sufficient number of trials per condition. The test set design is thus better suited to support high-fidelity decoding and robust representational similarity analysis.

We also added these explainations to our revised manuscript (line 161 to 164).

(8) "For Real-World Size RDM, we obtained human behavioral real-world size ratings of each object concept from the THINGS+ dataset (Stoinski et al., 2022).... The range of possible size ratings was from 0 to 519 in their online size rating task..." How were the ratings made? What is this scale - do people know the numbers? Was it on a continuous slider?

We should clarify how the real-world size values were obtained from the THINGS+ dataset.

In their experiment, participants first rated the size of a single object concept (word shown on the screen) by clicking on a continuous slider of 520 units, which was anchored by nine familiar real-world reference objects (e.g., “grain of sand,” “microwave oven,” “aircraft carrier”) that spanned the full expected size range on a logarithmic scale. Importantly, participants were not shown any numerical values on the scale—they were guided purely by the semantic meaning and relative size of the anchor objects. After the initial response, the scale zoomed in around the selected region (covering 160 units of the 520-point scale) and presented finer anchor points between the previous reference objects. Participants then refined their rating by dragging from the lower to upper end of the typical size range for that object. If the object was standardized in size (e.g., “soccer ball”), a single click sufficed. These size judgments were collected across at least 50 participants per object, and final scores were derived from the central tendency of these responses. Although the final size values numerically range from 0 to 519 (after scaling), this range is not known to participants and is only applied post hoc to construct the size RDMs.

We added these details in the Materials and Method section:

(line 219 to 230) “In the THINGS+ dataset, 2010 participants (different from the subjects in THINGS EEG2) did an online size rating task and completed a total of 13024 trials corresponding to 1854 object concepts using a two-step procedure. In their experiment, first, each object was rated on a 520unit continuous slider anchored by familiar reference objects (e.g., “grain of sand,” “microwave oven,” “aircraft carrier”) representing a logarithmic size range. Participants were not shown numerical values but used semantic anchors as guides. In the second step, the scale zoomed in around the selected region to allow for finer-grained refinement of the size judgment. Final size values were derived from aggregated behavioral data and rescaled to a range of 0–519 for consistency across objects, with the actual mean ratings across subjects ranging from 100.03 (‘grain of sand’) to 423.09 (‘subway’).”

(9) "For Retinal Size RDM, we applied Adobe Photoshop (Adobe Inc., 2019) to crop objects corresponding to object labels from images manually... " Was this by one person? Worth noting, and worth sharing these values per image if not already for other researchers as it could be a valuable resource (and increase citations).

Yes, all object cropping were performed consistently by one of the authors to ensure uniformity across images. We agree that this dataset could be a useful resource to the community. We have now made the cropped object images publicly available https://github.com/ZitongLu1996/RWsize.

We also updated the manuscript accordingly to note this (line 236 to 239).

(10) "Neural RDMs. From the EEG signal, we constructed timepoint-by-timepoint neural RDMs for each subject with decoding accuracy as the dissimilarity index " Decoding accuracy is presumably a similarity index. Maybe 1-accuracy (proportion correct) for dissimilarity?

Decoding accuracy is a dissimilarity index instead of a similarity index, as higher decoding accuracy between two conditions indicates that they are more distinguishable – i.e., less similar – in the neural response space. This approach aligns with prior work using classification-based representational dissimilarity measures (Grootswagers et al., 2017; Xie et al., 2020), where better decoding implies greater dissimilarity between conditions. Therefore, there is no need to invert the decoding accuracy values (e.g., using 1 - accuracy).

Grootswagers, T., Wardle, S. G., & Carlson, T. A. (2017). Decoding dynamic brain patterns from evoked responses: A tutorial on multivariate pattern analysis applied to time series neuroimaging data. Journal of Cognitive Neuroscience, 29(4), 677-697.

Xie, S., Kaiser, D., & Cichy, R. M. (2020). Visual imagery and perception share neural representations in the alpha frequency band. Current Biology, 30(13), 2621-2627.

(11) Figure 1 caption is very short - Could do with a more complete caption. Unclear what the partial correlations are (what is being partialled out in each case), what are the comparisons "between them" - both in the figure and the caption. Details should at least be in the main text.

Related to your comment (1). We revised the caption and the corresponding text.

Reviewer #2 (Recommendations For The Authors):

(1) Intro:

Quek et al., (2023) is referred to as a behavioral study, but it has EEG analyses.

We corrected this – “…, one recent study (Quek et al., 2023) …”

The phrase 'high temporal resolution EEG' is a bit strange - isn't all EEG high temporal resolution? Especially when down-sampling to 100 Hz (40 time points/epoch) this does not qualify as particularly high-res.

We removed this phrasing in our manuscript.

(2) Methods:

It would be good to provide more details on the EEG preprocessing. Were the data low-pass filtered, for example?

We added more details to the manuscript:

(line 167 to 174) “The EEG data were originally sampled at 1000Hz and online-filtered between 0.1 Hz and 100 Hz during acquisition, with recordings referenced to the Fz electrode. For preprocessing, no additional filtering was applied. Baseline correction was performed by subtracting the mean signal during the 100 ms pre-stimulus interval from each trial and channel separately. We used already preprocessed data from 17 channels with labels beginning with “O” or “P” (O1, Oz, O2, PO7, PO3, POz, PO4, PO8, P7, P5, P3, P1, Pz, P2) ensuring full coverage of posterior regions typically involved in visual object processing. The epoched data were then down-sampled to 100 Hz.”

It is important to provide more motivation about the specific ANN layers chosen. Were these layers cherry-picked, or did they truly represent a gradual shift over the course of layers?

We appreciate the reviewer’s concern and fully agree that it is important to ensure transparency in how ANN layers were selected. The early and late layers reported in the main text were not cherry-picked to maximize effects, but rather intended to serve as illustrative examples representing the lower and higher ends of the network hierarchy. To address this point directly, we have computed the EEG correlations with multiple layers in both ResNet and CLIP models (ResNet: ResNet.maxpool, ResNet.layer1, ResNet.layer2, ResNet.layer3, ResNet.layer4, ResNet.avgpool; CLIP: CLIP.visual.avgpool, CLIP.visual.layer1, CLIP.visual.layer2, CLIP.visual.layer3, CLIP.visual.layer4, CLIP.visual.attnpool). The results, now included in Figure S4, show a consistent trend: early layers exhibit higher similarity to early EEG time points, and deeper layers show increased similarity to later EEG stages.

It is important to provide more specific information about the specific ANN layers chosen. 'Second convolutional layer': is this block 2, the ReLu layer, the maxpool layer? What is the 'last visual layer'?

Apologize for the confusing! We added more details about the layer chosen:

(line 255 to 257) “The early layer in ResNet refers to ResNet.maxpool layer, and the late layer in ResNet refers to ResNet.avgpool layer. The early layer in CLIP refers to CLIP.visual.avgpool layer, and the late layer in CLIP refers to CLIP.visual.attnpool layer.”

Again the claim 'novel' is a bit overblown here since the real-world size ratings were also already collected as part of THINGS+, so all data used here is available.

We removed this phrasing in our manuscript.

Real-world size ratings ranged 'from 0 - 519'; it seems unlikely this was the actual scale presented to subjects, I assume it was some sort of slider?

You are correct. We should clarify how the real-world size values were obtained from the THINGS+ dataset.

In their experiment, participants first rated the size of a single object concept (word shown on the screen) by clicking on a continuous slider of 520 units, which was anchored by nine familiar real-world reference objects (e.g., “grain of sand,” “microwave oven,” “aircraft carrier”) that spanned the full expected size range on a logarithmic scale. Importantly, participants were not shown any numerical values on the scale—they were guided purely by the semantic meaning and relative size of the anchor objects. After the initial response, the scale zoomed in around the selected region (covering 160 units of the 520-point scale) and presented finer anchor points between the previous reference objects. Participants then refined their rating by dragging from the lower to upper end of the typical size range for that object. If the object was standardized in size (e.g., “soccer ball”), a single click sufficed. These size judgments were collected across at least 50 participants per object, and final scores were derived from the central tendency of these responses. Although the final size values numerically range from 0 to 519 (after scaling), this range is not known to participants and is only applied post hoc to construct the size RDMs.

We added these details in the Materials and Method section:

(line 219 to 230) “In the THINGS+ dataset, 2010 participants (different from the subjects in THINGS EEG2) did an online size rating task and completed a total of 13024 trials corresponding to 1854 object concepts using a two-step procedure. In their experiment, first, each object was rated on a 520unit continuous slider anchored by familiar reference objects (e.g., “grain of sand,” “microwave oven,” “aircraft carrier”) representing a logarithmic size range. Participants were not shown numerical values but used semantic anchors as guides. In the second step, the scale zoomed in around the selected region to allow for finer-grained refinement of the size judgment. Final size values were derived from aggregated behavioral data and rescaled to a range of 0–519 for consistency across objects, with the actual mean ratings across subjects ranging from 100.03 (‘grain of sand’) to 423.09 (‘subway’).”

Why is conducting a one-tailed (p<0.05) test valid for EEG-ANN comparisons? Shouldn't this be two-tailed?

Our use of one-tailed tests was based on the directional hypothesis that representational similarity between EEG and ANN RDMs would be positive, as supported by prior literature showing correspondence between hierarchical neural networks and human brain representations (e.g., Cichy et al., 2016; Kuzovkin et al., 2014). This is consistent with a large number of RSA studies which conduct one-tailed tests (i.e., testing the hypothesis that coefficients were greater than zero: e.g., Kuzovkin et al., 2018; Nili et al., 2014; Hebart et al., 2018; Kaiser et al., 2019; Kaiser et al., 2020; Kaiser et al., 2022). Thus, we specifically tested whether the similarity was significantly greater than zero.

Cichy, R. M., Khosla, A., Pantazis, D., Torralba, A., & Oliva, A. (2016). Comparison of deep neural networks to spatio-temporal cortical dynamics of human visual object recognition reveals hierarchical correspondence. Scientific reports, 6(1), 27755.

Kuzovkin, I., Vicente, R., Petton, M., Lachaux, J. P., Baciu, M., Kahane, P., ... & Aru, J. (2018). Activations of deep convolutional neural networks are aligned with gamma band activity of human visual cortex. Communications biology, 1(1), 107.

Nili, H., Wingfield, C., Walther, A., Su, L., Marslen-Wilson, W., & Kriegeskorte, N. (2014). A toolbox for representational similarity analysis. PLoS computational biology, 10(4), e1003553.

Hebart, M. N., Bankson, B. B., Harel, A., Baker, C. I., & Cichy, R. M. (2018). The representational dynamics of task and object processing in humans. Elife, 7, e32816.

Kaiser, D., Turini, J., & Cichy, R. M. (2019). A neural mechanism for contextualizing fragmented inputs during naturalistic vision. elife, 8, e48182.

Kaiser, D., Inciuraite, G., & Cichy, R. M. (2020). Rapid contextualization of fragmented scene information in the human visual system. Neuroimage, 219, 117045.

Kaiser, D., Jacobs, A. M., & Cichy, R. M. (2022). Modelling brain representations of abstract concepts. PLoS Computational Biology, 18(2), e1009837.

Importantly, we note that using a two-tailed test instead would not change the significance of our results. However, we believe the one-tailed test remains more appropriate given our theoretical prediction of positive similarity between ANN and brain representations.

The sentence on the partial correlation description (page 11 'we calculated partial correlations with one-tailed test against the alternative hypothesis that the partial correlation was positive (greater than zero)') didn't make sense to me; are you referring to the null hypothesis here?

We revised this sentence to clarify that we tested against the null hypothesis that the partial correlation was less than or equal to zero, using a one-tailed test to assess whether the correlation was significantly greater than zero.

(line 281 to 284) “…, we calculated partial correlations and used a one-tailed test against the null hypothesis that the partial correlation was less than or equal to zero, testing whether the partial correlation was significantly greater than zero.”

(3) Results:

I would prevent the use of the word 'pure', your measurement is one specific operationalization of this concept of real-world size that is not guaranteed to result in unconfounded representations. This is in fact impossible whenever one is using a finite set of natural stimuli and calculating metrics on those - there can always be a factor or metric that was not considered that could explain some of the variance in your measurement. It is overconfident to claim to have achieved some form of Platonic ideal here and to have taken into account all confounds.

Your point is well taken. Our original use of the term “pure” was intended to reflect statistical control for known confounding factors, but we recognize that this wording may imply a stronger claim than warranted. In response, we revised all relevant language in the manuscript to instead describe the statistically isolated or relatively unconfounded representation of real-world size, clarifying that our findings pertain to the unique contribution of real-world size after accounting for retinal size and real-world depth.

Figure 2C: It's not clear why peak latencies are computed on the 'full' correlations rather than the partial ones.

No. The peak latency results in Figure 2C were computed on the partial correlation results – we mentioned this in the figure caption – “Temporal latencies for peak similarity (partial Spearman correlations) between EEG and the 3 types of object information.”

SEM = SEM across the 10 subjects?

Yes. We added this in the figure caption.

Figure 3F y-axis says it's partial correlations but not clear what is partialled out here.

We identified and corrected a labeling error in both Figure 1 and Figure 3F. Specifically, our EEG × ANN analysis used Spearman correlation, not partial correlation as mistakenly indicated in the original figure label and text. We conducted parital correlations for EEG × HYP and ANN × HYP. But for EEG × ANN, we directly calculated the correlation between EEG RDMs and ANN RDM corresponding to different layers respectively. We corrected these errors: (1) In Figure 1, we removed the erroneous “partial” label from the EEG × ANN path and updated the caption to clearly outline which comparisons used partial correlation. (2) In Figure 3F, we corrected the Y-axis label to “(correlation)”.

Reviewer #3 (Recommendations For The Authors):

(1) Several methodologies should be clarified:

(a) It's stated that EEG was sampled at 100 Hz. I assume this was downsampled? From what original frequency?

Yes. We added more detailed about EEG data:

(line 167 to 174) “The EEG data were originally sampled at 1000Hz and online-filtered between 0.1 Hz and 100 Hz during acquisition, with recordings referenced to the Fz electrode. For preprocessing, no additional filtering was applied. Baseline correction was performed by subtracting the mean signal during the 100 ms pre-stimulus interval from each trial and channel separately. We used already preprocessed data from 17 channels with labels beginning with “O” or “P” (O1, Oz, O2, PO7, PO3, POz, PO4, PO8, P7, P5, P3, P1, Pz, P2) ensuring full coverage of posterior regions typically involved in visual object processing. The epoched data were then down-sampled to 100 Hz.”

(b) Why was decoding accuracy used as the human RDM method rather than the EEG data themselves?

Thanks for your question! We would like to address why we used decoding accuracy for EEG RDMs rather than correlation. While fMRI RDMs are typically calculated using 1 minus correlation coefficient, decoding accuracy is more commonly used for EEG RDMs (Grootswager et al., 2017; Xie et al., 2020). The primary reason is that EEG signals are more susceptible to noise than fMRI data. Correlation-based methods are particularly sensitive to noise and may not reliably capture the functional differences between EEG patterns for different conditions. Decoding accuracy, by training classifiers to focus on task-relevant features, can effectively mitigate the impact of noisy signals and capture the representational difference between two conditions.

Grootswagers, T., Wardle, S. G., & Carlson, T. A. (2017). Decoding dynamic brain patterns from evoked responses: A tutorial on multivariate pattern analysis applied to time series neuroimaging data. Journal of Cognitive Neuroscience, 29(4), 677-697.

Xie, S., Kaiser, D., & Cichy, R. M. (2020). Visual imagery and perception share neural representations in the alpha frequency band. Current Biology, 30(13), 2621-2627.

We added this explanation to the manuscript:

(line 204 to 209) “Since EEG has a low SNR and includes rapid transient artifacts, Pearson correlations computed over very short time windows yield unstable dissimilarity estimates (Kappenman & Luck, 2010; Luck, 2014) and may thus fail to reliably detect differences between images. In contrast, decoding accuracy - by training classifiers to focus on task-relevant features - better mitigates noise and highlights representational differences.”

(c) How were the specific posterior electrodes selected?

The 17 posterior electrodes used in our analyses were pre-selected and provided in the THINGS EEG2 dataset, and corresponding to standard occipital and parietal sites based on the 10-10 EEG system. Specifically, we included all 17 electrodes with labels beginning with “O” or “P”, ensuring full coverage of posterior regions typically involved in visual object processing (Page 7).

(d) The specific layers should be named rather than the vague ("last visual")

Apologize for the confusing! We added more details about the layer information:

(line 255 to 257) “The early layer in ResNet refers to ResNet.maxpool layer, and the late layer in ResNet refers to ResNet.avgpool layer. The early layer in CLIP refers to CLIP.visual.avgpool layer, and the late layer in CLIP refers to CLIP.visual.attnpool layer.”

(line 420 to 434) “As shown in Figure 3F, the early layer representations of both ResNet and CLIP (ResNet.maxpool layer and CLIP.visual.avgpool) showed significant correlations with early EEG time windows (early layer of ResNet: 40-280ms, early layer of CLIP: 50-130ms and 160-260ms), while the late layers (ResNet.avgpool layer and CLIP.visual.attnpool layer) showed correlations extending into later time windows (late layer of ResNet: 80-300ms, late layer of CLIP: 70-300ms). Although there is substantial temporal overlap between early and late model layers, the overall pattern suggests a rough correspondence between model hierarchy and neural processing stages.

We further extended this analysis across intermediate layers of both ResNet and CLIP models (from early to late, ResNet: ResNet.maxpool, ResNet.layer1, ResNet.layer2, ResNet.layer3, ResNet.layer4, ResNet.avgpool; from early to late, CLIP: CLIP.visual.avgpool, CLIP.visual.layer1, CLIP.visual.layer2, CLIP.visual.layer3, CLIP.visual.layer4, CLIP.visual.attnpool).”

(e) p19: please change the reporting of t-statistics to standard APA format.

Thanks for the suggestion. We changed the reporting format accordingly:

(line 392 to 394) “The representation of real-word size had a significantly later peak latency than that of both retinal size, t(9)=4.30, p=.002, and real-world depth, t(9)=18.58, p<.001. And retinal size representation had a significantly later peak latency than real-world depth, t(9)=3.72, p=.005.”

(2) "early layer of CLIP: 50-130ms and 160-260ms), while the late layer representations of twoANNs were significantly correlated with later representations in the human brain (late layer of ResNet: 80-300ms, late layer of CLIP: 70-300ms)."

This seems a little strong, given the large amount of overlap between these models.

We agree that our original wording may have overstated the distinction between early and late layers, given the substantial temporal overlap in their EEG correlations. We revised this sentence to soften the language to reflect the graded nature of the correspondence, and now describe the pattern as a general trend rather than a strict dissociation:

(line 420 to 427) “As shown in Figure 3F, the early layer representations of both ResNet and CLIP (ResNet.maxpool layer and CLIP.visual.avgpool) showed significant correlations with early EEG time windows (early layer of ResNet: 40-280ms, early layer of CLIP: 50-130ms and 160-260ms), while the late layers (ResNet.avgpool layer and CLIP.visual.attnpool layer) showed correlations extending into later time windows (late layer of ResNet: 80-300ms, late layer of CLIP: 70-300ms). Although there is substantial temporal overlap between early and late model layers, the overall pattern suggests a rough correspondence between model hierarchy and neural processing stages.”

(3) "Also, human brain representations showed a higher similarity to the early layer representation of the visual model (ResNet) than to the visual-semantic model (CLIP) at an early stage. "

This has been previously reported by Greene & Hansen, 2020 J Neuro.

Thanks! We added this reference.

(4) "ANN (and Word2Vec) model RDMs"

Why not just "model RDMs"? Might provide more clarity.

We chose to use the phrasing “ANN (and Word2Vec) model RDMs” to maintain clarity and avoid ambiguity. In the literature, the term “model RDMs” is sometimes used more broadly to include hypothesis-based feature spaces or conceptual models, and we wanted to clearly distinguish our use of RDMs derived from artificial neural networks and language models. Additionally, explicitly referring to ANN or Word2Vec RDMs improves clarity by specifying the model source of each RDM. We hope this clarification justifies our choice to retain the original phrasing for clarity.

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

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Reply to the reviewers

General Statements

We would like to thank the referees for their time and effort in giving feedback on our work, and their overall positive attitude towards the manuscript. Most of the referees' points were of clarifying and textual nature. We have identified three points which we think require more attention in the form of additional analyses, simulations or significant textual changes:

Within the manuscript we state that conserved non coding sequences (CNSs) are a proxy for cis regulatory elements (CREs). We proceed to use these terms interchangeably without explaining the underlying assumption, which is inaccurate. To improve on this point we ensured in the new text that we are explicit about when we mean CNS or CRE. Secondly, we added a section to the discussion (‘Limitations of CNSs as CREs’) dedicated to this topic. During stabilising selection (maintaining the target phenotype) DSD can occur fully neutrally, or through the evolution of either mutational or developmental robustness. We describe the evolutionary trajectories of our simulations as neutral once fitness mostly plateaued; however, as reviewer 3 points out, small gains in median fitness still occur, indicating that either development becomes more robust to noisy gene expression and tissue variation, and/or the GRNs become more robust to mutations. To discern between fully neutral evolution where the fitness distribution of the population does not change, and the higher-order emergence of robustness, we performed additional analysis of the given results. Preliminary results showed that many (near-)neutral mutations affect the mutational robustness and developmental robustness, both positively and negatively. To investigate this further we will run an additional set of simulations without developmental stochasticity, which will take about a week. These simulations should allow us to more closely examine the role of stabilising selection (of developmental robustness) in DSD by removing the need to evolve developmental robustness. Additionally, we will set up simulations in which we changed the total number of genes, and the number of genes under selection to investigate how this modelling choice influences DSD. In the section on rewiring (‘Network redundancy creates space for rewiring’) we will analyse the mechanism allowing for rewiring in more depth, especially in the light of gene duplications and redundancy. We will extend this section with an additional analysis aimed to highlight how and when rewiring is facilitated. We will describe the planned and incorporated revisions in detail below; we believe these have led to a greatly improved manuscript.

Kind regards,

Pjotr van der Jagt, Steven Oud and Renske Vroomans

Description of the planned revisions

Referee cross commenting (Reviewer 4)

Reviewer 3's concern about DSD resulting from stabilising selection for robustness is something I missed -- this is important and should be addressed.

We understand this concern, and agree that we should be more thorough in our analysis of DSD by assessing the higher-order effects of stabilising selection on mutational robustness and/or environmental (developmental) robustness (McColgan & DiFrisco 2024).

We will 1) extend our analysis of fitness under DSD by computing the mutational and developmental robustness (similar to Figure 2F) over time for a number of ancestral lineages. By comparing these two measures over evolutionary time we will gain a much more fine grained image of the evolutionary dynamics and should be able to find adaptive trends through gain of either type of robustness. Preliminary results suggest that during the plateaued fitness phase both mutational robustness and developmental robustness undergo weak gains and losses, likely due to the pleiotropic nature of our GPM. Collectively, these weak gains and losses result in the gain observed in Figure S3. So, rather than fully neutral we should discern (near-)neutral regimes in which clear adaptive steps are absent, but in which the sum of them is a net gain. These are interesting findings we initially missed, and give insights into how this high-dimensional fitness landscape is traversed, and will be included in a future revised version of the manuscript.

2) We will run extra simulations without stochasticity to investigate DSD in the absence of adaptation through developmental robustness, and include the comparison between these and our original simulations in a future revised version.

Finally 3) we will address stabilising selection more prominently in the introduction and discussion to accommodate these additional simulations.

Reviewer 3 suggests that the model construction may favor DSD because there are many genes (14) of which only two determine fitness. I agree that some discussion on this point is warranted, though I am not sure enough is known about "the possible difference in constraints between the model and real development" for such a discussion to be on firm biological footing. A genetic architecture commonly found in quantitative genetic studies is that a small number of genes have large effects on the phenotype/fitness, whereas a very large number of genes have effects that are individually small but collectively large (see, e.g. literature surrounding the "omnigenic model" of complex traits). Implementing such an architecture is probably beyond the scope of the study here. More generally, would be natural to assume that the larger the number of genes, and the smaller the number of fitness-determining genes, the more likely DSD / re-wiring is to occur. That being said, I think the authors' choice of a 14-gene network is biologically defensible. It could be argued that the restriction of many modeling studies to small networks (often including just 3 genes) on the ground of convenience artificially ensures that DSD will not occur in these networks.

The choice of 14 genes does indeed stem from a compromise between constraining the number of available genes, but at the same time allowing for sufficient degrees of freedom and redundancy. We have added a ‘modelling choices’ section in the discussion in which we address this point. Additionally, it is important to note that, while the fitness criterion only measures the pattern of 2 genes, throughout the evolutionary lineage additional genes become highly important for the fitness of an individual, because these genes evolved to help generate the target pattern (see for example Figure 4); the other genes indeed reflect reviewer 4’s point that most genes have a small effect. Crucially, we observe that even the genes and interactions that are important for fitness undergo DSD.

Nevertheless, we think it is interesting to investigate this point of the influence of this particular modelling choice on the potential for DSD, and have set up an extra set of simulations with fewer gene types, and one with additional fitness genes.

Furthermore, we discuss the choice of our network architecture more in depth in a discussion section on our modelling choices: ‘Modelling assumptions and choices’.

Reviewer 1

The observation of DSD in the computational models remains rather high-level in the sense that no motifs, mechanisms, subgraphs, mutations or specific dynamics are reported to be associated to it ---with the exception of gene expression domains overlapping. Perhaps the authors feel it is beyond this study, but a Results section with a more in-depth "mechanistic" analysis on what enables DSD would (a) make a better case for the extensive and expensive computational models and (b) would push this paper to a next level. As a starting point, it could be nice to check Ohno's intuition that gene duplications are a creative "force" in evolution. Are they drivers of DSD? Or are TFBS mutations responsible for the majority of cases?

We agree that some mechanistic analysis would strengthen the manuscript, and will therefore extend the section ‘Network redundancy creates space for rewiring’ to address how this redundancy is facilitated. For instance, in the rewiring examples given in Figure 4 we can highlight how this new interaction emerges, if this is through a gene mutation followed by rewiring and loss of a redundant gene, or if the gain, redundancy and loss are all on the level of TFBS mutations. Effectively we will investigate which route of the three in the following schematic is most prominent:

Additionally, we will do analysis on the different effects of the transcription dynamics for each of these routes. (note that this is not an exhaustive schematic, and combinations could be possible).

l171. You discuss an example here, would it be possible to generalize this analysis and quantify the amount of DSD amongst all cloned populations? And related question: of the many conserved interactions in Fig 4A, how many do the two clonal lineages share? None? All?

We agree that this is a good idea. In a new supplementary figure, we will show the number of times a conserved interaction gets lost, and a new interaction is gained as a metric for DSD in every cloned population.

The populations in Fig 4A are cloned at generation 50.000, any interaction starting before then and still present at a point in time is shared. Any interactions starting after 50.000 are unique (or independently gained at least).

- l269. What about phenotypic plasticity due to stochastic gene expression? Does it play a role in DSD in your model? I am thinking about https://pubmed.ncbi.nlm.nih.gov/24884746/ and https://pubmed.ncbi.nlm.nih.gov/21211007/

We agree that this is an interesting point which should be included into the discussion. Following the comments of reviewer 3 we have set up extra simulations to investigate this in more detail, we will make sure to include these citations in the revised discussion when we have the results of those simulations.

Reviewer 3

Issue One: Interpretation of fitness gains under stabilising selection

A central issue concerns how the manuscript defines and interprets developmental systems drift (DSD) in relation to evolution on the fitness landscape. The authors define DSD as the conservation of a trait despite changes in its underlying genetic basis, which is consistent with the literature. However, the manuscript would benefit from clarifying the relationship between DSD, genotype-to-phenotype maps, and fitness landscapes. Very simply, we can say that (i) DSD can operate along neutral paths in the fitness landscape, (ii) DSD can operate along adaptive paths in the fitness landscape. During DSD, these neutral or adaptive paths along the fitness landscape are traversed by mutations that change the gene regulatory network (GRN) and consequent gene expression patterns whilst preserving the developmental outcome, i.e., the phenotype. While this connection between DSD and fitness landscapes is referenced in the introduction, it is not fully elaborated upon. A complete elaboration is critical because, when I read the manuscript, I got the impression that the manuscript claims that DSD is prevalent along neutral paths in the fitness landscape, not just adaptive ones. If I am wrong and this is not what the authors claim, it should be explicitly stated in the results and discussed. Nevertheless, claiming DSD operates along neutral paths is a much more interesting statement than claiming it operates along adaptive paths. However, it requires sufficient evidence, which I have an issue with.

The issue I have is about adaptations under stabilising selection. Stabilising selection occurs when there is selection to preserve the developmental outcome. Stabilising selection is essential to the results because evolutionary change in the GRN under stabilising selection should be due to DSD, not adaptations that change the developmental outcome. To ensure that the populations are under stabilising selection, the authors perform clonal experiments for 100,000 generations for 8 already evolved populations, 5 clones for each population. They remove 10 out of 40 clones because the fitness increase is too large, indicating that the developmental outcome changes over the 100,000 generations. However, the remaining 30 clonal experiments exhibit small but continual fitness increases over 100,000 generations. The authors claim that the remaining 30 are predominantly evolving due to drift, not adaptations (in the main text, line 137: "indicating predominantly neutral evolution", and section M: "too shallow for selection to outweigh drift"). The author's evidence for this claim is a mathematical analysis showing that the fitness gains are too small to be caused by beneficial adaptations, so evolution must be dominated by drift. I found this explanation strange, given that every clone unequivocally increases in fitness throughout the 100,000 generations, which suggests populations are adapting. Upon closer inspection of the mathematical analysis (section M), I believe it will miss many kinds of adaptations possible in their model, as I now describe.

The mathematical analysis treats fitness as a constant, but it's a random variable in the computational model. Fitness is a random variable because gene transcription and protein translation are stochastic (Wiener terms in Eqs. (1)-(5)) and cell positions change for each individual (Methods C). So, for a genotype G, the realised fitness F is picked from a distribution with mean μ_G and higher order moments (e.g., variance) that determine the shape of the distribution. I think these assumptions lead to two problems.

The first problem with the mathematical analysis is that F is replaced by an absolute number f_q, with beneficial mutations occurring in small increments denoted "a", representing an additive fitness advantage. The authors then take a time series of the median population fitness from their simulations and treat its slope as the individual's additive fitness advantage "a". The authors claim that drift dominates evolution because this slope is lower than a drift-selection barrier, which they derive from the mathematical analysis. This analysis ignores that the advantage "a" is a distribution, not a constant, which means that it does not pick up adaptations that change the shape of the distribution. Adaptations that change the shape of the distribution can be adaptations that increase robustness to stochasticity. Since there are multiple sources of noise in this model, I think it is highly likely that robustness to noise is selected for during these 100,000 generations.

The second problem is that the mathematical analysis ignores traits that have higher-order effects on fitness. A trait has higher-order effects when it increases the fitness of the lineage (e.g., offspring) but not the parent. One possible trait that can evolve in this model with higher-order effects is mutational robustness, i.e., traits that lower the expected mutational load of descendants. Since many kinds of mutations occur in this model (Table 2), mutational robustness may be also evolving.

Taken together, the analysis in Section M is set up to detect only immediate, deterministic additive gains in a single draw of fitness. It therefore cannot rule out weak but persistent adaptive evolution of robustness (to developmental noise and/or to mutations), and is thus insufficient evidence that DSD is occurring along neutral paths instead of adaptive paths. The small but monotonic fitness increases observed in all 40 clones are consistent with such adaptation (Fig. S3). The authors also acknowledge the evolution of robustness in lines 129-130 and 290-291, but the possibility of these adaptations driving DSD instead of neutral evolution is not discussed.

To address the issue I have with adaptations during stabilising selection, the authors should, at a minimum, state clearly in their results that DSD is driven by both the evolution of robustness and drift. Moreover, a paragraph in the discussion should be dedicated to why this is the case, and why it is challenging to separate DSD through neutral evolution vs DSD through adaptations such as those that increase robustness.

[OPTIONAL] A more thorough approach would be to make significant changes to the manuscript by giving sufficient evidence that the experimental clones are evolving by drift, or changing the model construction. One possible way to provide sufficient evidence is to improve the mathematical analysis. Another way is to show that the fitness distributions (both without and with mutations, like in Fig. 2F) do not significantly change throughout the 100,000 generations in experimental clones. It seems more likely that the model construction makes it difficult to separate the evolution of robustness from evolution by drift in the stabilising selection regime. Thus, I think the model should be constructed differently so that robustness against mutations and noise is much less likely to evolve after a "fitness plateau" is reached. This could be done by removing sources of noise from the model or reducing the kinds of possible mutations (related to issue two). In fact, I could not find justification in the manuscript for why these noise terms are included in the model, so I assume they are included for biological realism. If this is why noise is included, or if there is a separate reason why it is necessary, please write that in the model overview and/or the methods.

We agree that we should be more precise about whether DSD operates along neutral vs adaptive paths in the fitness landscape, and have expanded our explanation of this distinction in the introduction. We also agree that it is worthwhile to distinguish between neutral evolution that does not change the fitness distribution of the population (either through changes in developmental or mutational robustness), higher-order evolutionary processes that increase developmental robustness, and drift along a neutral path in the fitness landscape towards regions of greater connectivity, resulting in mutational robustness (as described in Huynen et al., 1999). We have performed a preliminary analysis to identify changes in mutational robustness and developmental robustness over evolutionary time in the populations in which the maximum fitness has already plateaued. This analysis shows frequent weak gains and losses, in which clear adaptive steps are absent but a net gain can be seen in robustness, as consistent with higher-order fitness effects.

To investigate the role of stabilising selection more in depth we will run simulations without developmental noise in the form of gene expression noise and tissue connectivity variation, thus removing the effect of the evolution of developmental robustness. We will compare the evolutionary dynamics of the GRNs with our original set of simulations, and include both these types of analyses in a supplementary figure of the revised manuscript.

Furthermore, we now discuss the limitations of the mathematical analysis with regard to adaptation vs neutrality in our simulations, in the supplementary section.

Issue two: The model construction may favour DSD

In this manuscript, fitness is determined by the expression pattern of two types of genes (genes 12 and 13 in Table 1). There are 14 types of genes in total that can all undergo many kinds of mutations, including duplications (Table 2). Thus, gene regulatory networks (GRNs) encoded by genomes in this model tend to contain large numbers of interactions. The results show that most of these interactions have minimal effect on reaching the target pattern in high fitness individuals (e.g. Fig. 2F). A consequence of this is that only a minimal number of GRN interactions are conserved through evolution (e.g. Fig. 2D). From these model constructions and results from evolutionary simulations, we can deduce that there are very few constraints on the GRN. By having very few constraints on the GRN, I think it makes it easy for a new set of pattern-producing traits to evolve and subsequently for an old set of pattern-producing traits to be lost, i.e., DSD. Thus, I believe that the model construction may favour DSD.

I do not have an issue with the model favouring DSD because it reflects real multicellular GRNs, where it is thought that a minority fraction of interactions are critical for fitness and the majority are not. However, it is unknown whether the constraints GRNs face in the model are more or less constrained than real GRNs. Thus, it is not known whether the prevalence of DSD in this model applies generally to real development, where GRN constraints depend on so many factors. At a minimum, the possible difference in constraints between the model and real development should be discussed as a limitation of the model. A more thorough change to the manuscript would be to test the effect of changing the constraints on the GRN. I am sure there are many ways to devise such a test, but I will give my recommendation here.

[OPTIONAL] My recommendation is that the authors should run additional simulations with simplified mutational dynamics by constraining the model to N genes (no duplications and deletions), of which M out of these N genes contribute to fitness via the specific pattern (with M=2 in the current model). The authors should then test the effect of changing N and M independently, and how this affects the prevalence of DSD. If the prevalence of DSD is robust to changes in N and M, it supports the authors argument that DSD is highly prevalent in developmental evolution. If DSD prevalence is highly dependent on M and/or N, then the claims made in the manuscript about the prevalence of DSD must change accordingly. I acknowledge that these simulations may be computationally expensive, and I think it would be great if the authors knew (or devised) a more efficient way to test the effect of GRN constraints on DSD prevalence. Nevertheless, these additional simulations would make for a potentially very interesting manuscript.

We agree that these modelling choices likely influence the potential for DSD. We think that our model setup, where most transcription factors are not under direct selection for a particular pattern, more accurately reflects biological development, where the outcome of the total developmental process (a functional organism) is what is under selection, rather than each individual gene pattern. As also mentioned by the referee, in real multicellular development the majority of interactions is not crucial for fitness, similar to our model. We also observe that, as fitness increases, additional genes experience emergent selection for particular expression patterns or interaction structures in the GRN, resulting in their conservation. Nevertheless, we do agree that the effect of model construction on DSD is an unexplored avenue and this work lends itself to addressing this. We will run additional sets of simulations: one in which we reduce the size of the network (‘N’), and a second set where we double the number of fitness contributing genes (‘M’), and show the effect on the extent of DSD in a future supplementary figure.

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

Referee cross commenting (Reviewer 4)

Overall I agree with the comments of Reviewer 1, 2 and 3. I note that reviewers 1, 3, and 4 each pointed out the difficulties with assuming that CNSs = CREs, so this needs to be addressed. Two reviewers (3 and 4) also point out problems with equating bulk RNAseq with a conserved phenotype.

We agree that caution is warranted with the assumption of CNSs = CREs. We have added a section to the discussion in which we discuss this more thoroughly, see ‘Limitations of CNSs as CREs’ in the revised manuscript.

Additionally, we made textual changes to the statement of significance, abstract and results to better reflect when we talk about CNSs or CREs.

I agree with Reviewer 1's hesitancy about the rhetorical framing of the paper potentially generalising too far from a computational model of plant meristem patterning.

We agree that the title should reflect the scope of the manuscript, and our short title reflects that better than ubiquitous, which implies we investigated beyond plant (meristem) development. We have changed the title in the revised version, to ‘System drift in the evolution of plant meristem development’.

Reviewer 1

It is system drift, not systems drift (see True and Haag 2001). No 's' after system.

Thank you for catching this – we corrected this throughout.

- I am afraid I have a problem with the manuscript title. I think "Ubiquitoes" is misplaced, because it strongly suggests you have a long list of case studies across plants and animals, and some quantification of DSD in these two kingdoms. That would have been an interesting result, but it is not what you report. I suggest something along the lines of "System drift in the evolution of plant meristem development", similar to the short title used in the footer.

- Alternatively, the authors may aim to say that DSD happens all over the place in computational models of development? In that case the title should reflect that the claim refers to modeling. (But what then about the data analysis part?)

As remarked in the summary (point 2), we agree with this assessment and have changed the title to ‘System drift in the evolution of plant meristem development’’

Multiple times in the Abstract and Introduction the authors make statements on "cis-regulatory elements" that are actually "conserved non-coding sequences" (CNS). Even if it is not uncommon for CNSs to harbor enhancers etc., I would be very hesitant to use the two as synonyms. As the authors state themselves, sequences, even non-coding, can be conserved for many reasons other than CREs. I would ask the authors to support better their use of "CREs" or adjust language. As roughly stated in their Discussion (lines 310-319), one way forward could be to show for a few CNS that are important in the analysis (of Fig 5), that they have experimentally-verified enhancers. Is that do-able or a bridge too far?

We changed the text such that we use CNS instead of CRE when discussing the bioinformatic analysis. Additionally we added a section in the discussion to clarify the relationship between CNS and CRE.

line 7. evo-devo is jargon

We changed this to ‘…evolution of development (evo-devo) research…’

l9. I would think "using a computational model and data analysis"

Yes, corrected.

l13. Strictly speaking you did not look at CREs, but at conserved non-coding sequences.

Indeed, we changed this to CNS.

l14. "widespread" is exaggerated here, since you show for a single organ in a handful of plant species. You may extrapolate and argue that you do not see why it should not be widespread, but you did not show it. Or tie in all the known cases that can be found in literature.

We understand that ‘widespread’ seems to suggest that we have investigated a broader range of species and organs. To be more accurate we changed the wording to ‘prevalent’.

l16. "simpler" than what?

We added the example of RNA folding.

l27. Again the tension between CREs and non-coding sequence.

Changed to conserved non coding sequence.

l28. I don't understand the use of "necessarily" here.

This is indeed confusing and unnecessary, removed

l34-35. A very general biology statement is backed up by two modeling studies. I would have expected also a few based on comparative analyses (e.g., fossils, transcriptomics, etc).

We added extra citations and a discussion of more experimental work

l36. I was missing the work on "phenogenetic drift" by Weiss; and Pavlicev & Wagner 2012 on compensatory mutations.

Changed the text to:

This phenomenon is called developmental system drift (DSD) (True and Haag, 2001; McColgan and DiFrisco, 2024), or phenogenetic drift (Weiss and Fullerton, 2000), and can occur when multiple genotypes which are separated by few mutational steps encode the same phenotype, forming a neutral (Wagner, 2008a; Crombach et al., 2016); or adaptive path (Johnson and Porter, 2007; Pavlicev and Wagner, 2012) .

l38. Kimura and Wagner never had a developmental process in mind, which is much bigger than a single nucleotide or a single gene, respectively. First paper that I am aware of that explicitly connects DSD to evolution on genotype networks is my own work (Crombach 2016), since the editor of that article (True, of True and Haag 2001) highlighted that point in our communications.

Added citation and moved Kimura to the theoretical examples of protein folding DSD.

l40. While Hunynen and Hogeweg definitely studied the GP map in many of their works, the term goes back to Pere Alberch (1991).

Added citation.

l54-55. I'm missing some motivation here. If one wants to look at multicellular structures that display DSD, vulva development in C. elegans and related worms is an "old" and extremely well-studied example. Also, studies on early fly development by Yogi Jaeger and his co-workers are not multicellular, but at least multi-nuclear. Obviously these are animal-based results, so to me it would make sense to make a contrast animal-plant regarding DSD research and take it from there.

Indeed, DSD has been found in these species and we now reference some of this work; the principle is better known in animals. Nevertheless, within the theoretical literature there is a continuing debate on the importance/extent of DSD.

Changed text:

‘For other GPMs, such as those resulting from multicellular development, it has been suggested that complex phenotypes are sparsely distributed in genotype space, and have low potential for DSD because the number of neutral mutations anti-correlates with phenotypic complexity (Orr, 2000; Hagolani et al., 2021). On the other hand, theoretical and experimental studies in nematodes and fruit flies have shown that DSD is present in a phenotypically complex context (Verster et al., 2014; Crombach et al., 2016; Jaeger, 2018). It therefore remains debated how much DSD actually occurs in species undergoing multicellular development. DSD in plants has received little attention. One multicellular structure which …’

l66-86. It is a bit of a style-choice, but this is a looong summary of what is to come. I would not have done that. Instead, in the Introduction I would have expected a bit more digging into the concept of DSD, mention some of the old animal cases, perhaps summarize where in plants it should be expected. More context, basically.

We extended the paragraph on empirical examples of DSD by adding the animal cases and condensed our summary.

l108. Could you quantify the conserved interactions shared between the populations? Or is each simulation so different that they are pretty much unique?

Each simulation here is independent of the other simulations, so a per interaction comparison would be uninformative. After cloning they do share ancestry, but that is much later in the manuscript and here the quantification of the conserved interactions would be the inverse of the divergence as shown in, for instance Figure 3B.

l169. "DSD driving functional divergence" needs some context, since DSD is supposed to not affect function (of the final phenotype). Or am I misunderstanding?

This is indeed a confusing sentence. We mean to say that DSD allows for divergence to such an extent that the underlying functional pathway is changed. So instead of a mere substitution of the underlying network, in which the topology and relative functions stay conserved, a different network structure is found. We have modified the line to read “Taken together, we found that DSD can drive functional divergence in the underlying GRN resulting in novel spatial expression dynamics of the genes not directly under selection.”

l176. Say which interaction it is. Is it 0->8, as mentioned in the next paragraph?

It is indeed 0->8, we have clarified this in the text.

l197. Bulk RNAseq has the problem of averaging gene expression over the population of cells. How do you think that impacts your test for rewiring? If you would do a similar "bulk RNA" style test on your computational models, would you pick up DSD?

The rewiring is based on the CNSs, whereas the RNAseq is used as phenotype, so it does not impact the test for rewiring.

The averaging of bulk RNAseq does however, mean that we cannot show conservation/divergence of the phenotype within the tissues, only between the different tissues.

The most important implication of doing this in our model would be the definition of the ‘phenotype’ which undergoes DSD. Currently the phenotype is a gene expression pattern on a cellular level, for bulk RNA this phenotype would change to tissue-level gene expression.

This change in what we measure as phenotype implicates how we interpret our results, but would not hinder us in picking up DSD, it just has a different meaning than DSD on a cellular - and single tissue scale.

We added clarification of the roles of the datasets at the start of the paragraph.

‘The Conservatory Project collects conserved non-coding sequences (CNSs) across plant genomes, which we used to investigate the extent of GRN rewiring in flowering plants. Schuster et al. measured gene expression in different homologous tissues of several species via bulk RNAseq, which we used to test for gene expression (phenotype) conservation, and how this relates to the GRN rewiring inferred from the CNSs.’

l202. I do not understand the "within" of a non-coding sequence within an orthogroup. How are non-coding sequences inside an orthogroup of genes?

We clarify this sentence by saying ‘A CNS is defined as a non-coding sequence conserved within the upstream/downstream region of genes within an orthogroup’, to more clearly separate the CNS from the orthogroup of genes. We also updated Figure 5A to reflect this better.

l207-217. This paragraph is difficult to read and would benefit of a rephrasing. Plant-specific jargon, numbers do not add up (line 211), statements are rather implicit (9 deeply conserved CNS are the 3+6? Where do I see them in Fig 5B? And where do I see the lineage-specific losses?).

We added extra annotations to the figure to make the plant jargon (angiosperm, eudicot, Brassicaceae) clear, and show the loss more clearly in the figure. We also clarified the text by splitting up 9 to 3 and 6.

l223. Looking at the shared CNS between SEP1-2, can you find a TF binding site or another property that can be interpreted as regulatory importance?

Reliably showing an active TF binding site would require experimental data, which we don’t have. We do mention in the discussion the need for datasets which could help address this gap.

l225. My intuition says that the continuity of the phenotype may not be necessary if its loss can be compensated for somehow by another part of the organism. I.e., DSD within DSD. It is a poorly elaborated thought, I leave it here for your information. Perhaps a Discussion point?

Although very interesting we think this discussion might be outside of the scope of this work, and would benefit from a standalone discussion – especially since the capacity for such compensation might differ between animals and plants (which are more “modular” organisms). This is our interpretation:

First, let’s take a step back from ‘genotype’ and ‘phenotype’ and redefine DSD more generally: in a system with multiple organisational levels, where a hierarchical mapping between them exists, DSD is changes on one organisational level which do not alter the outcome of the ‘higher’ organisational level. In other words, DSD can exist any many-to-one mapping in which a set of many (which map to the same one) are within a certain distance in space, which we generally define as a single mutational step.

Within this (slightly) more general definition we can extend the definition of DSD to the level of phenotype and function, in which phenotype describes the ‘many’ layer, and multiple phenotypes can fulfill the same function. When we are freed from the constraint of ‘genotype’ and ‘phenotype’, and DSD is defined at the level of this mapping, than it becomes an easy exercise to have multiple mappings (genotype→phenotype→function) and thus ‘DSD within DSD’.

l233. "rarely"? I don't see any high Pearson distances.

True in the given example there are no high Pearson distances, however some of the supplementary figures do so rarely felt like the most honest description. We changed the text to refer to these supplementary figures.

Fig 4. Re-order of panels? I was expecting B at C and vice versa.

Agreed, we swapped the order of the panels

Fig 5B. Red boxes not explained. Mention that it is an UpSetplot?

We added clarification to the figure caption.

Fig 5D. It would be nice to quantify the minor and major diffs between orthologs and paralogs.

We quantify the similarities (and thus differences) in Figure F, but we do indeed not show orthologs vs paralogs explicitly. We have extended Figure F to distinguish which comparisons are between orthologs vs paralogs with different tick marks, which shows their different distributions quite clearly.

- l247. Over-generalization. In a specific organ of plants...

Changed to vascular plant meristem.

- l249. Where exactly is this link between diverse expression patterns and the Schuster dataset made? I suggest the authors to make it more explicit in the Results.

We are slightly overambitious in this sentence. The Schuster dataset confirms the preservation of expression where the CNS dataset shows rewiring. That this facilitates diversification of expression patterns in traits not under selection is solely an outcome of the computational model. We have changed the text to reflect this more clearly.

- l268. Final sentence of the paragraph left me puzzled. Why talk about opposite function?

The goal here was to highlight regulatory rewiring which, in the most extreme case, would achieve an opposite function for a given TF within development. We agree that this was formulated vaguely so we rewrote this to be more to the point.

These examples demonstrate that whilst the function of pathways is conserved, their regulatory wiring often is not.

- l269. What about time scales generated by the system? Looking at Fig 2C and 2D, the elbow pattern is pretty obvious. That means interactions sort themselves into either short-lived or long-lived. Worth mentioning?

Added a sentence to highlight this.

- l291. Evolution in a *constant* fitness landscape increases robustness.

Changed

- l296. My thoughts, for your info: I suspect morphogenesis as single parameters instead of as mechanisms makes for a brittle landscape, resulting in isolated parts of the same phenotype.

We agree, and now include citations to different models in which morphogenesis evolves which seem to display a more connected landscape.

Reviewer 2

Every computational model necessarily makes some simplifying assumptions. It would be nice if the authors could summarise in a paragraph in the Discussion the main assumptions made by their model, and which of those are most worth revisiting in future studies. In the current draft, some assumptions are described in different places in the manuscript, which makes it hard for a non-expert to evaluate the limitations of this model.

We added a section to the discussion: ‘Modelling assumptions and choices’

I did not find any mention of potential energetic constraints or limitations in this model. For example, I would expect high levels of gene expression to incur significant energy costs, resulting in evolutionary trade-offs. Could the authors comment on how taking energy limitations into account might influence their results?

This would put additional constraints on the evolution/fitness landscape. Some paths/regions of the fitness landscape which are currently accessible will not be traversable anymore. On the other hand, an energy constraint might reduce certain high fitness areas to a more even plane and thus make it more traversable. During analysis of our data there were no signs of extremely high gene expression levels.

Figure 3C lists Gene IDs 1, 2, 8, and 11, but the caption refers to genes 1, 2, 4, and 11.

Thank you for catching this.

Reviewer 3

The authors present an analysis correlating conserved non-coding sequence (CNS) composition with gene expression to investigate developmental systems drift. One flaw of this analysis is that it uses deeply conserved sequences as a proxy for the entire cis-regulatory landscape. The authors acknowledge this flaw in the discussion.

Another potential flaw is equating the bulk RNA-seq data with a conserved phenotype. In lines 226-227 of the manuscript, it is written that "In line with our computational model, we compared gene expression patterns to measure changes in phenotype." I am not sure if there is an equivalence between the two. In the computational model, the developmental outcome determining fitness is a spatial pattern, i.e., an emergent product of gene expression and cell interactions. In contrast, the RNA-seq data shows bulk measurements in gene expression for different organs. It is conceivable that, despite having very similar bulk measurements, the developmental outcome in response to gene expression (such as a spatial pattern or morphological shape) changes across species. I think this difference should be explicitly addressed in the discussion. The authors may have intended to discuss this in lines 320-326, although it is unclear to me.

It is correct that the CNS data and RNA-seq data has certain limitations, and the brief discussion of some of these limitations in lines 320-326 is not sufficient. We have been more explicit on this point in the discussion.

The gene expression data used in this study represents bulk expression at the organ level, such as the vegetative meristem (Schuster et al., 2024). This limits our analysis of the phenotypic effects of rewiring to comparisons between organs, which is different to our computational simulations where we look at within organ gene expression. Additionally, the bulk RNA-seq does not allow us to discern whether the developmental outcome of similar gene expression is the same in all these species. More fine-grained approaches, such as single-cell RNA sequencing or spatial transcriptomics, will provide a more detailed understanding of how gene expression is modulated spatially and temporally within complex tissues of different organisms, allowing for a closer alignment between computational predictions and experimental observations.

Can the authors justify using these six species in the discussion or the results? Are there any limitations with choosing four closely related and two distantly related species for this analysis, in contrast to, say, six distantly related species? If so, please elaborate in the discussion.

The use of these six species is mainly limited by the datasets we have available. Nevertheless, the combination of four closely related species, and two more distantly related species gives a better insight into the short vs long term divergence dynamics than six distantly related species would. We have noted this when introducing the datasets:

This set of species contains both closely (A. thaliana, A. lyrata, C. rubella, E. salsugineum) and more distantly related species (M. truncatula, B. distachyon), which should give insight in short and long term divergence.

In Figure S7, some profiles show no conservation across the six species. Can we be sure that a stabilising selection pressure conserves any CNSs? Is it possible that the deeply conserved CNSs mentioned in the main text are conserved by chance, given the large number of total CNSs? A brief comment on these points in the results or discussion would be helpful.

In our simulations, we find that even CREs that were under selection for a long time can disappear; however, in our neutral simulations, CREs were not conserved, suggesting that deep conservation is the result of selection. When it comes to CNSs, the assumption is that they often contain CREs that are under selection.We have added a more elaborate section on CNSs in the discussion. See ‘Limitations of CNSs as CREs’

Line 7-8: I thought this was a bit difficult to read. The connection between (i) evolvability of complex phenotypes, (ii) neutral/beneficial change hindered by deleterious mutations, and (iii) DSD might not be so simple for many readers, so I think it should be rewritten. The abstract was well written, though.

We made the connection to DSD and evolvability clearer and removed the specific mutational outcomes:

*A key open question in evolution of development (evo-devo) is the evolvability of complex phenotypes. Developmental system drift (DSD) may contribute to evolvability by exploring different genotypes with similar phenotypic outcome, but with mutational neighbourhoods that have different, potentially adaptive, phenotypes. We investigated the potential for DSD in plant development using a computational model and data analysis. *

Line 274 vs 276: Is there a difference between regulatory dynamics and regulatory mechanisms?

No, we should use the same terminology. We have changed this to be clearer.

Figure S4: Do you expect the green/blue lines to approach the orange line in the long term? In some clonal experiments, it seems like it will. In others, it seems like it has plateaued. Under continual DSD, I assume they should converge. It would be interesting to see simulations run sufficiently long to see if this occurs.

In principle yes, however this might take a considerable amount of time given that some conserved interactions take >75000 generations to be rewired.

Line 27: Evolutionarily instead of evolutionary?

Changed

Line 67-68: References in brackets?

Changed

Line 144: Capitalise "fig"

Changed

Fig. 3C caption: correct "1, 2, 4, 11" (should be 8)

Changed

Line 192: Reference repeated

Changed

Fig. 5 caption: Capitalise "Supplementary figure"

Changed

Line 277: Correct "A previous model Johnson.."

Changed

Line 290: Brackets around reference

Changed

Line 299: Correct "will be therefore be"

Changed

Line 394: Capitalise "table"

Changed

Line 449: Correct "was build using"

Changed

Fig. 5B: explain the red dashed boxes in the caption

Added explanation to the caption

Some of the Figure panels might benefit from further elaboration in their respective captions, such as 3C and 5F.

Improved the figure captions.

Reviewer 4

Statement of significance. The logical connection between the first two sentences is not clear. What does developmental system drift have to do with neutral/beneficial mutations?

This is indeed an unclear jump. Changed such that the connection between evolvability of complex phenotypes and DSD is more clear:

*A key open question in evolution of development (evo-devo) is the evolvability of complex phenotypes. Developmental system drift (DSD) contributes to evolvability by exploring different genotypes with similar phenotypic outcome, but with mutational neighbourhoods that have different, potentially adaptive, phenotypes..We investigated the potential for DSD in plant development using a computational model and data analysis. *

l 41 - "DSD is found to ... explain the developmental hourglass." Caution is warranted here. Wotton et al 2015 claim that "quantitative system drift" explains the hourglass pattern, but it would be more accurate to say that shifting expression domains and strengths allows compensatory regulatory change to occur with the same set of genes (gap genes). It is far from clear how DSD could explain the developmental hourglass pattern. What does DSD imply about the causes of differential conservation of different developmental stages? It's not clear there is any connection here.

We should indeed be more cautious here. DSD is indeed not in itself an explanation of the hourglass model, but only a mechanism by which the developmental divergence observed in the hourglass model could have emerged. As per Pavlicev and Wagner, 2012, compensatory changes resulting from other shifts would fall under DSD, and can explain how the patterning outcome of the gap gene network is conserved. However, this does not explain why some stages are under stronger selection than others. We changed the text to reflect this.

‘...be a possible evolutionary mechanism involved in the developmental hourglass model (Wotton et al., 2015; Crombach et al., 2016)...’

ll 51-53 - "Others have found that increased complexity introduces more degrees of freedom, allowing for a greater number of genotypes to produce the same phenotype and potentially allowing for more DSD (Schiffman and Ralph, 2022; Greenbury et al., 2022)." Does this refer to increased genomic complexity or increased phenotypic complexity? It is not clear that increased phenotypic complexity allows a greater number of genotypes to produce the same phenotype. Please explain further.

The paragraph discusses complexity in the GPM as a whole, where the first few examples in the paragraph regard phenotypic complexity, and the ones in l51-53 refer to genomic complexity. This is currently not clear so we clarified the text.

‘For other GPMs, such as those resulting from multicellular development, it has been suggested that complex phenotypes are sparsely distributed in genotype space, and have low potential for DSD because the number of neutral mutations anti-correlates with phenotypic complexity (Orr, 2000; Hagolani et al., 2021). Others have found that increased genomic complexity introduces more degrees of freedom, allowing for a greater number of genotypes to produce the same phenotype and potentially allowing for more DSD (Schiffman and Ralph, 2022; Greenbury et al., 2022).’

It was not clear why some gene products in the model have the ability to form dimers. What does this contribute to the simulation results? This feature is introduced early on, but is not revisited. Is it necessary?

*Fitness. The way in which fitness is determined in the model was not completely clear to me. *

Dimers are not necessary, but as they have been found to play a role in actual SAM development we added them to increase the realism of the developmental simulations. In some simulations the patterning mechanism involves the dimer, in others it does not, suggesting that dimerization is not essential for DSD.

We have made changes to the methods to clarify fitness.

Lines 103-104 say: "Each individual is assigned a fitness score based on the protein concentration of two target genes in specific regions of the SAM: one in the central zone (CZ), and one in the organizing center (OC)." How are these regions positionally defined in the simulation?

We have defined bounding boxes to define cells as either CZ, OC or both. We have added these bounds in the figure description and more clearly in the revised methods.

F, one reads (l. 385): "Fitness depends on the correct protein concentration of the two fitness genes in each cell, pcz and poc respectively." This sounds like fitness is determined by the state of all cells rather than the state of the two specific regions of the SAM. Please clarify.

A fitness penalty is given for incorrect expression so it is true that the fitness is determined by the state of all cells. We agree that it is phrased unclearly and have clarified this in the text.

The authors use conserved non-coding sequences as a proxy for cis-regulatory elements. More specification of how CNSs were assigned to an orthogroup seems necessary in this section. Is assignment based on proximity to the coding region? Of course the authors will appreciate that regulatory elements can be located far from the gene they regulate. This data showed extensive gains and losses of CNS. It might be interesting to consider how much of this is down to transposons, in which case rapid rearrangement is not unexpected. A potential problem with the claim that the data supports the simulation results follows from the fact that DSD is genetic divergence despite trait conservation, but conserved traits appear to have only been defined or identified in the case of the SEP genes. It can't be ruled out that divergence in CNSs and in gene expression captured by the datasets is driven by straightforward phenotypic adaptation, thus not by DSD. Further caution on this point is needed.

CNSs are indeed assigned based on proximity up to 50kb, the full methods are described in detail in Hendelman et al., (2021). CREs can be located further than 50kb, but evidence suggests that this is rare for species with smaller genomes.

In the cases where both gene expression and the CNSs diverged it can indeed not be ruled out that there has been phenotypic adaptation. We clarified in the text that the lower Pearson distances are informative for DSD as they highlight conserved phenotypes.

l. 290-291 - "However, evolution has been shown to increase mutational robustness over time, resulting in the possibility for more neutral change." It is doubtful that there is any such unrestricted trend. If mutational robustness only tended to increase, new mutations would not affect the phenotype, and phenotypes would be unable to adapt to novel environments. Consider rethinking this statement.

We have reformulated this statement, since it is indeed not expected that this trend is indefinite. Infinite robustness would indeed result in the absence of evolvability; however, it has been shown for other genotype-phenotype maps that mutational robustness, where a proportion of mutations is neutral, aids the evolution of novel traits. The evolution of mutational robustness also depends on population size and mutation rate. This trend will, most probably, also be stronger in modelling work where the fitness function is fixed, compared to a real life scenario where ‘fitness’ is much less defined and subject to continuous change. We added ‘constant’ to the fitness landscape to highlight this disparity.

ll. 316-317 "experimental work investigating the developmental role of CREs has shown extensive epistasis - where the effect of a mutation depends on the genetic background - supporting DSD." How does extensive epistasis support DSD? One can just as easily imagine scenarios where high interdependence between genes would prevent DSD from occurring. Please explain further.

We should be more clear. Experimental work has shown that the effect of mutating a particular CRE strongly depends on the genetic background, also known as epistasis. Counterintuitively, this indirectly supports the presence of DSD, since it means that different species or strains have slightly different developmental mechanisms, resulting in these different mutational effects. We have shown how epistatic effects shift over evolutionary time.

Overall I found the explanation of the Methods, especially the formal aspects, to be unclear at times and would recommend that the authors go back over the text to improve its clarity.

We rewrote parts of the methods and some of the equations to be more clear and cohesive throughout the text.

C. Tissue Generation. Following on the comment on fitness above, it would be advisable to provide further details on how cell positions are defined. How much do the cells move over the course of the simulation? What is the advantage of modelling the cells as "springs" rather than as a simple grid?

The tissue generation is purely a process to generate a database of tissue templates: the random positions, springs and voronoi method serve the purpose of having similar but different tissues to prevent unrealistic overfitting of our GRNs on a single topology. For each individual’s development however, only one, unchanging template is used. We clarified this in the methods.

E. Development of genotype into phenotype. The diffusion term in the SDE equations is hard to understand as no variable for spatial position (x) is included in the equation. It seems this equation should rather be an SPDE with a position variable and a specified boundary condition (i.e. the parabola shape). In eq. 5 it should be noted that the Wi are independent. Also please justify the choice of how much noise/variance is being stipulated here.

We have rewritten parts of this section for clarity and added citations.

F. Fitness function. I must say I found formula 7 to be unclear. It looks like fi is the fitness of cell(s) but, from Section G, fitness is a property of the individual. It seems formula 7 should define fi as a sum over the cell types or should capture the fitness contribution of the cell types.

Correct. We have rewritten this equation. We’ll define fi as the fitness contribution of a cell, F as the sum of fi, so the fitness of an individual, and use F in function 8.

What is the basis for the middle terms (fractions) in the equation? After plugging in the values for pcz and poc, this yields a number, but how does that number assign a cell to one of the types? If a reviewer closely scrutinizing this section cannot make sense of it, neither will readers. Please explain further.

The cell type is assigned based on the spatial location of the cell, and the correct fitness function for each of these cell types is described in this equation. We have clarified the text and functions.

A minor note: it would be best practice not to re-use variables to refer to different things within the same paper. For example p refers to protein concentration but also probability of mutation.

Corrected

This work has been peer reviewed in GigaScience (see https://doi.org/10.1093/gigascience/giaf126), which carries out open, named peer-review. These reviews are published under a CC-BY 4.0 license and were as follows:

Reviewer 2: Jérôme Salignon

This manuscript presents tcga-data-nf, a Nextflow-based pipeline for downloading, preprocessing, and analyzing TCGA multi-omic data, with a focus on gene regulatory network (GRN) inference. The workflow integrates established bioinformatics tools (PANDA, DRAGON, and LIONESS) and adheres to best practices for reproducibility through containerization (Docker, Conda, and Nextflow profiles). The authors demonstrate the utility of their pipeline by applying it to colorectal cancer subtypes, identifying potential regulatory interactions in TGF-β signaling. The manuscript is well-written and well-structured and provides sufficient methodological details, as well as Jupyter notebooks, for reproducibility. However, there are some areas that require clarification and improvement for acceptance in GigaScience, particularly regarding the scope of the tool, the quality of the inferred regulatory networks, the case study figure, benchmarking, statistical validation, and parameters.

Major comments:

• While the pipeline is well designed and executed, the overall impact of the tool feels somewhat limited, especially for a journal like GigaScience, due to its pretty specific application to building GRNs in TCGAs, the relatively small number of parameters, the support of only 2 omics type, and the lack of novel algorithms. To increase the impact of this tool I would recommend adding functionalities, such as:

o Supporting additional tools. A great strength of the pipeline is the integration with the Network Zoo (NetZoo) ecosystem. However, only three tools are included from NetZoo. Including additional tools would likely increase the scope of users interested in using the pipeline. In particular, an important weakness of the current pipeline is that it is not possible to conduct differential analysis between different networks, which prevents users from identifying the most significant differences between two networks of interest (e.g., CMS2 vs CMS4). The NetZoo contains different tools to conduct such analyses, such as Alpaca 1 or Crane 2, thus this may be implemented to make the pipeline more useful to a broader user base.

o Adding parameters. A strength of the pipeline is the ability to customize it using various parameters. However, as such the pipeline does not offer many parameters. It would be beneficial to make the pipeline a bit more customizable. For example, novel parameters could be: adding options for excluding selected samples, using different batch correction methods, different methods to map CpGs to genes, additional normalization methods, and additional quality controls (e.g., PCA for methylation samples, md5sum checks). These are just examples and do not need to be all implemented but adding some extra parameters would help make the pipeline more appealing and customizable to various users.

• The quality of the inferred regulatory networks is hard to judge. There are no direct comparisons with any other tools.

o For instance, it is mentioned in the text that GRAND networks were derived using a fixed set of parameters, but it could be helpful to show a direct comparison between GRNs built from your tools with those from GRAND. This could reveal how the ability to customize GRNs using the pipeline's parameters helps in getting better biological insights.

o Alternatively, or in addition, one could compare how networks built by your method fare in comparison to networks built from other methods, like RegEnrich 3 or NetSeekR 4, in terms of biological insights, accuracy, scalability, speed, functionalities and/or memory usage.

o Another angle to judge the regulatory networks would be to check in a case study if the predicted gene interactions between disease and control networks are enriched in disease and gene-gene interactions databases, such as DisGeNet 5.

• Figure 2 needs re-work:

o Panel A and C: text is too small. "tf" should be written TF. "oi" should have another name. These panels might be moved to the supplements.

o Panel D is confusing. Without significance it is hard to understand what the point of this panel is. I can see that certain TFs are cited in the main text but without information about significance, these may seem like cherry-picking. The legends states: Annotation of all TFs in cluster D (columns) to the Reactome parent term. "Immune system" and "Cellular respondes to stimuli" are more consistenly involved in cluster D, in comparison to cluster A.. However, this is a key result which should be shown in a main figure, not in Figure S6. I would also recommend using a -log scale when displaying the p-values to highlight the most significant entries.

o Panel E is quite confusing; first, the color coding is unclear. For instance, what represents blue, purple and red colors? Second, what represents the edges' widths? I would recommend using different shapes for the methylation and expression nodes to reduce the number of colors, and adding a color legend. I would also consider merging the two graphs and representing in color the difference in the edge values so the reader can directly see the key differences.

• Benchmarking analysis could be included to show the runtime and memory requirement for each pipeline step. It would also be beneficial to analyze a larger dataset than colon cancer to assess the scalability.

• Statistical analysis: If computationally feasible, permutation testing could be implemented to quantify the robustness of inferred regulatory interactions. Also, in the method section, it should be clarified that FDR correction was applied for pathway enrichment analysis.

Minor comments:

• I am not sure why duplicate samples are discarded in the pipeline. Why not add counts for RNA-Seq and averaging beta values? I would expect that to yield more robust results.

• It is a bit unclear in what context the NetworkDataCompanion tool could be used outside the workflow. It is also unclear how it helps with quality controls. Please clarify these aspects.

• The manuscript is well-written, but words are sometimes missing or wrongly written, it needs careful re-read.

• The expression '"same-same"' is unclear to me.

• In this sentence: "Some of "same-same" genes (STAT5A, CREB3L1"…, I am not sure in which table or figure I can find this result?

• Text is too small in the Directed Acyclic Graph, especially in Figure S4. Also, I would recommend adding the Directed Acyclic Graphs from Figure S1-S4 to the online documentation.

• Regarding the code, I was puzzled to see a copyConfigFiles process. Also, there are files in bin/r/local_assets, these should be located in assets. And the container for the singularity and docker profile is likely the same, this should be clarified in the code.

• It is recommended to remove the "defaults" channel from the list of channels declared in the containers/conda_envs/analysis.yml file. Please see information about that here https://www.anaconda.com/blog/is-conda-free and here https://www.theregister.com/2024/08/08/anaconda_puts_the_squeeze_on/.

Additional comments (which do not need to be addressed):

• Future work may consider enabling the use of the pipeline to build GRNs from other data sources than TCGA (i.e., nf-netzoo). Recount3 data is already being parsed for GTEx and TCGA samples, so it might be relatively easy to adapt the pipeline so that it can be used on any arbitrary recount3 dataset. Similarly, it could be useful if one could specify a dataset on the recountmethylation database 6 to build GRNs. While these unimodal datasets could not be used with the DRAGON method they would still benefit from all other features of the pipeline.

• Using a nf-core template would enable better structure of the code and increase the visibility of the tool. Also using multiple containers is usually easier to maintain and update than a single large container, especially when a single tool needs to be updated or when modifying part of the pipeline. Another comment is that the code contains many comments which are not to explain the code but more like quick draft which makes the code harder to read by others.

References 1. Padi, M., and Quackenbush, J. (2018). Detecting phenotype-driven transitions in regulatory network structure. npj Syst Biol Appl 4, 1-12. https://doi.org/10.1038/s41540-018-0052-5. 2. Lim, J.T., Chen, C., Grant, A.D., and Padi, M. (2021). Generating Ensembles of Gene Regulatory Networks to Assess Robustness of Disease Modules. Front. Genet. 11. https://doi.org/10.3389/fgene.2020.603264. 3. Tao, W., Radstake, T.R.D.J., and Pandit, A. (2022). RegEnrich gene regulator enrichment analysis reveals a key role of the ETS transcription factor family in interferon signaling. Commun Biol 5, 1-12. https://doi.org/10.1038/s42003-021-02991-5. 4. Srivastava, H., Ferrell, D., and Popescu, G.V. (2022). NetSeekR: a network analysis pipeline for RNA-Seq time series data. BMC Bioinformatics 23, 54. https://doi.org/10.1186/s12859-021-04554-1. 5. Hu, Y., Guo, X., Yun, Y., Lu, L., Huang, X., and Jia, S. (2025). DisGeNet: a disease-centric interaction database among diseases and various associated genes. Database 2025, baae122. https://doi.org/10.1093/database/baae122. 6. Maden, S.K., Walsh, B., Ellrott, K., Hansen, K.D., Thompson, R.F., and Nellore, A. (2023). recountmethylation enables flexible analysis of public blood DNA methylation array data. Bioinformatics Advances 3, vbad020. https://doi.org/10.1093/bioadv/vbad020.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

This study investigates the sex determination mechanism in the clonal ant Ooceraea biroi, focusing on a candidate complementary sex determination (CSD) locus-one of the key mechanisms supporting haplodiploid sex determination in hymenopteran insects. Using whole genome sequencing, the authors analyze diploid females and the rarely occurring diploid males of O. biroi, identifying a 46 kb candidate region that is consistently heterozygous in females and predominantly homozygous in diploid males. This region shows elevated genetic diversity, as expected under balancing selection. The study also reports the presence of an lncRNA near this heterozygous region, which, though only distantly related in sequence, resembles the ANTSR lncRNA involved in female development in the Argentine ant, Linepithema humile (Pan et al. 2024). Together, these findings suggest a potentially conserved sex determination mechanism across ant species. However, while the analyses are well conducted and the paper is clearly written, the insights are largely incremental. The central conclusion - that the sex determination locus is conserved in ants - was already proposed and experimentally supported by Pan et al. (2024), who included O. biroi among the studied species and validated the locus's functional role in the Argentine ant. The present study thus largely reiterates existing findings without providing novel conceptual or experimental advances.

Although it is true that Pan et al., 2024 demonstrated (in Figure 4 of their paper) that the synteny of the region flanking ANTSR is conserved across aculeate Hymenoptera (including O. biroi), Reviewer 1’s claim that that paper provides experimental support for the hypothesis that the sex determination locus is conserved in ants is inaccurate. Pan et al., 2024 only performed experimental work in a single ant species (Linepithema humile) and merely compared reference genomes of multiple species to show synteny of the region, rather than functionally mapping or characterizing these regions.

Other comments:

The mapping is based on a very small sample size: 19 females and 16 diploid males, and these all derive from a single clonal line. This implies a rather high probability for false-positive inference. In combination with the fact that only 11 out of the 16 genotyped males are actually homozygous at the candidate locus, I think a more careful interpretation regarding the role of the mapped region in sex determination would be appropriate. The main argument supporting the role of the candidate region in sex determination is based on the putative homology with the lncRNA involved in sex determination in the Argentine ant, but this argument was made in a previous study (as mentioned above).

Our main argument supporting the role of the candidate region in sex determination is not based on putative homology with the lncRNA in L. humile. Instead, our main argument comes from our genetic mapping (in Fig. 2), and the elevated nucleotide diversity within the identified region (Fig. 4). Additionally, we highlight that multiple genes within our mapped region are homologous to those in mapped sex determining regions in both L. humile and Vollenhovia emeryi, possibly including the lncRNA.

In response to the Reviewer’s assertion that the mapping is based on a small sample size from a single clonal line, we want to highlight that we used all diploid males available to us. Although the primary shortcoming of a small sample size is to increase the probability of a false negative, small sample sizes can also produce false positives. We used two approaches to explore the statistical robustness of our conclusions. First, we generated a null distribution by randomly shuffling sex labels within colonies and calculating the probability of observing our CSD index values by chance (shown in Fig. 2). Second, we directly tested the association between homozygosity and sex using Fisher’s Exact Test (shown in Supplementary Fig. S2). In both cases, the association of the candidate locus with sex was statistically significant after multiple-testing correction using the Benjamini-Hochberg False Discovery Rate. These approaches are clearly described in the “CSD Index Mapping” section of the Methods.

We also note that, because complementary sex determination loci are expected to evolve under balancing selection, our finding that the mapped region exhibits a peak of nucleotide diversity lends orthogonal support to the notion that the mapped locus is indeed a complementary sex determination locus.

The fourth paragraph of the results and the sixth paragraph of the discussion are devoted to explaining the possible reasons why only 11/16 genotyped males are homozygous in the mapped region. The revised manuscript will include an additional sentence (in what will be lines 384-388) in this paragraph that includes the possible explanation that this locus is, in fact, a false positive, while also emphasizing that we find this possibility to be unlikely given our multiple lines of evidence.

In response to Reviewer 1’s suggestion that we carefully interpret the role of the mapped region in sex determination, we highlight our careful wording choices, nearly always referring to the mapped locus as a “candidate sex determination locus” in the title and throughout the manuscript. For consistency, the revised manuscript version will change the second results subheading from “The O. biroi CSD locus is homologous to another ant sex determination locus but not to honeybee csd” to “O. biroi’s candidate CSD locus is homologous to another ant sex determination locus but not to honeybee csd,” and will add the word “candidate” in what will be line 320 at the beginning of the Discussion, and will change “putative” to “candidate” in what will be line 426 at the end of the Discussion.

In the abstract, it is stated that CSD loci have been mapped in honeybees and two ant species, but we know little about their evolutionary history. But CSD candidate loci were also mapped in a wasp with multi-locus CSD (study cited in the introduction). This wasp is also parthenogenetic via central fusion automixis and produces diploid males. This is a very similar situation to the present study and should be referenced and discussed accordingly, particularly since the authors make the interesting suggestion that their ant also has multi-locus CSD and neither the wasp nor the ant has tra homologs in the CSD candidate regions. Also, is there any homology to the CSD candidate regions in the wasp species and the studied ant?

In response to Reviewer 1’s suggestion that we reference the (Matthey-Doret et al. 2019) study in the context of diploid males being produced via losses of heterozygosity during asexual reproduction, the revised manuscript will include (in what will be lines 123-126) the highlighted portion of the following sentence: “Therefore, if O. biroi uses CSD, diploid males might result from losses of heterozygosity at sex determination loci (Fig. 1C), similar to what is thought to occur in other asexual Hymenoptera that produce diploid males (Rabeling and Kronauer 2012; Matthey-Doret et al. 2019).”

We note, however, that in their 2019 study, Matthey-Doret et al. did not directly test the hypothesis that diploid males result from losses of heterozygosity at CSD loci during asexual reproduction, because the diploid males they used for their mapping study came from inbred crosses in a sexual population of that species.

We address this further below, but we want to emphasize that we do not intend to argue that O. biroi has multiple CSD loci. Instead, we suggest that additional, undetected CSD loci is one possible explanation for the absence of diploid males from any clonal line other than clonal line A. In response to Reviewer 1’s suggestion that we reference the (Matthey-Doret et al. 2019) study in the context of multilocus CSD, the revised manuscript version will include the following additional sentence in the fifth paragraph of the discussion (in what will be lines 372-374): “Multi-locus CSD has been suggested to limit the extent of diploid male production in asexual species under some circumstances (Vorburger 2013; Matthey-Doret et al. 2019).”

Regarding Reviewer 2’s question about homology between the putative CSD loci from the (Matthey-Doret et al. 2019) study and O. biroi, we note that there is no homology. The revised manuscript version will have an additional Supplementary Table (which will be the new Supplementary Table S3) that will report the results of this homology search. The revised manuscript will also include the following additional sentence in the Results, in what will be lines 172-174: “We found no homology between the genes within the O. biroi CSD index peak and any of the genes within the putative L. fabarum CSD loci (Supplementary Table S3).”

The authors used different clonal lines of O. biroi to investigate whether heterozygosity at the mapped CSD locus is required for female development in all clonal lines of O. biroi (L187-196). However, given the described parthenogenesis mechanism in this species conserves heterozygosity, additional females that are heterozygous are not very informative here. Indeed, one would need diploid males in these other clonal lines as well (but such males have not yet been found) to make any inference regarding this locus in other lines.

We agree that a full mapping study including diploid males from all clonal lines would be preferable, but as stated earlier in that same paragraph, we have only found diploid males from clonal line A. We stand behind our modest claim that “Females from all six clonal lines were heterozygous at the CSD index peak, consistent with its putative role as a CSD locus in all O. biroi.” In the revised manuscript version, this sentence (in what will be lines 199-201) will be changed slightly in response to a reviewer comment below: “All females from all six clonal lines (including 26 diploid females from clonal line B) were heterozygous at the CSD index peak, consistent with its putative role as a CSD locus in all O. biroi.”

Reviewer #2 (Public review):

The manuscript by Lacy et al. is well written, with a clear and compelling introduction that effectively conveys the significance of the study. The methods are appropriate and well-executed, and the results, both in the main text and supplementary materials, are presented in a clear and detailed manner. The authors interpret their findings with appropriate caution.

This work makes a valuable contribution to our understanding of the evolution of complementary sex determination (CSD) in ants. In particular, it provides important evidence for the ancient origin of a non-coding locus implicated in sex determination, and shows that, remarkably, this sex locus is conserved even in an ant species with a non-canonical reproductive system that typically does not produce males. I found this to be an excellent and well-rounded study, carefully analyzed and well contextualized.

That said, I do have a few minor comments, primarily concerning the discussion of the potential 'ghost' CSD locus. While the authors acknowledge (line 367) that they currently have no data to distinguish among the alternative hypotheses, I found the evidence for an additional CSD locus presented in the results (lines 261-302) somewhat limited and at times a bit difficult to follow. I wonder whether further clarification or supporting evidence could already be extracted from the existing data. Specifically:

We agree with Reviewer 2 that the evidence for a second CSD locus is limited. In fact, we do not intend to advocate for there being a second locus, but we suggest that a second CSD locus is one possible explanation for the absence of diploid males outside of clonal line A. In our initial version, we intentionally conveyed this ambiguity by titling this section “O. biroi may have one or multiple sex determination loci.” However, we now see that this leads to undue emphasis on the possibility of a second locus. In the revised manuscript, we will split this into two separate sections: “Diploid male production differs across O. biroi clonal lines” and “O. biroi lacks a tra-containing CSD locus.”

(1) Line 268: I doubt the relevance of comparing the proportion of diploid males among all males between lines A and B to infer the presence of additional CSD loci. Since the mechanisms producing these two types of males differ, it might be more appropriate to compare the proportion of diploid males among all diploid offspring. This ratio has been used in previous studies on CSD in Hymenoptera to estimate the number of sex loci (see, for example, Cook 1993, de Boer et al. 2008, 2012, Ma et al. 2013, and Chen et al., 2021). The exact method might not be applicable to clonal raider ants, but I think comparing the percentage of diploid males among the total number of (diploid) offspring produced between the two lineages might be a better argument for a difference in CSD loci number.

We want to re-emphasize here that we do not wish to advocate for there being two CSD loci in O. biroi. Rather, we want to explain that this is one possible explanation for the apparent absence of diploid males outside of clonal line A. We hope that the modifications to the manuscript described in the previous response help to clarify this.

Reviewer 2 is correct that comparing the number of diploid males to diploid females does not apply to clonal raider ants. This is because males are vanishingly rare among the vast numbers of females produced. We do not count how many females are produced in laboratory stock colonies, and males are sampled opportunistically. Therefore, we cannot report exact numbers. However, we will add the highlighted portion of the following sentence (in what will be lines 268-270) to the revised manuscript: “Despite the fact that we maintain more colonies of clonal line B than of clonal line A in the lab, all the diploid males we detected came from clonal line A.”

(2) If line B indeed carries an additional CSD locus, one would expect that some females could be homozygous at the ANTSR locus but still viable, being heterozygous only at the other locus. Do the authors detect any females in line B that are homozygous at the ANTSR locus? If so, this would support the existence of an additional, functionally independent CSD locus.

We thank the reviewer for this suggestion, and again we emphasize that we do not want to argue in favor of multiple CSD loci. We just want to introduce it as one possible explanation for the absence of diploid males outside of clonal line A.

The 26 sequenced diploid females from clonal line B are all heterozygous at the mapped locus, and the revised manuscript will clarify this in what will be lines 199-201. Previously, only six of those diploid females were included in Supplementary Table S2, and that will be modified accordingly.

(3) Line 281: The description of the two tra-containing CSD loci as "conserved" between Vollenhovia and the honey bee may be misleading. It suggests shared ancestry, whereas the honey bee csd gene is known to have arisen via a relatively recent gene duplication from fem/tra (10.1038/nature07052). It would be more accurate to refer to this similarity as a case of convergent evolution rather than conservation.

In the sentence that Reviewer 2 refers to, we are representing the assertion made in the (Miyakawa and Mikheyev 2015) paper in which, regarding their mapping of a candidate CSD locus that contains two linked tra homologs, they write in the abstract: “these data support the prediction that the same CSD mechanism has indeed been conserved for over 100 million years.” In that same paper, Miyakawa and Mikheyev write in the discussion section: “As ants and bees diverged more than 100 million years ago, sex determination in honey bees and V. emeryi is probably homologous and has been conserved for at least this long.”

As noted by Reviewer 2, this appears to conflict with a previously advanced hypothesis: that because fem and csd were found in Apis mellifera, Apis cerana, and Apis dorsata, but only fem was found in Mellipona compressipes, Bombus terrestris, and Nasonia vitripennis, that the csd gene evolved after the honeybee (Apis) lineage diverged from other bees (Hasselmann et al. 2008). However, it remains possible that the csd gene evolved after ants and bees diverged from N. vitripennis, but before the divergence of ants and bees, and then was subsequently lost in B. terrestris and M. compressipes. This view was previously put forward based on bioinformatic identification of putative orthologs of csd and fem in bumblebees and in ants [(Schmieder et al. 2012), see also (Privman et al. 2013)]. However, subsequent work disagreed and argued that the duplications of tra found in ants and in bumblebees represented convergent evolution rather than homology (Koch et al. 2014). Distinguishing between these possibilities will be aided by additional sex determination locus mapping studies and functional dissection of the underlying molecular mechanisms in diverse Aculeata.

Distinguishing between these competing hypotheses is beyond the scope of our paper, but the revised manuscript will include additional text to incorporate some of this nuance. We will include these modified lines below (in what will be lines 287-295), with the additions highlighted:

“A second QTL region identified in V. emeryi (V.emeryiCsdQTL1) contains two closely linked tra homologs, similar to the closely linked honeybee tra homologs, csd and fem (Miyakawa and Mikheyev 2015). This, along with the discovery of duplicated tra homologs that undergo concerted evolution in bumblebees and ants (Schmieder et al. 2012; Privman et al. 2013) has led to the hypothesis that the function of tra homologs as CSD loci is conserved with the csd-containing region of honeybees (Schmieder et al. 2012; Miyakawa and Mikheyev 2015). However, other work has suggested that tra duplications occurred independently in honeybees, bumblebees, and ants (Hasselmann et al. 2008; Koch et al. 2014), and it remains to be demonstrated that either of these tra homologs acts as a primary CSD signal in V. emeryi.”

(4) Finally, since the authors successfully identified multiple alleles of the first CSD locus using previously sequenced haploid males, I wonder whether they also observed comparable allelic diversity at the candidate second CSD locus. This would provide useful supporting evidence for its functional relevance.

As is already addressed in the final paragraph of the results and in Supplementary Fig. S4, there is no peak of nucleotide diversity in any of the regions homologous to V.emeryiQTL1, which is the tra-containing candidate sex determination locus (Miyakawa and Mikheyev 2015). In the revised manuscript, the relevant lines will be 307-310. We want to restate that we do not propose that there is a second candidate CSD locus in O. biroi, but we simply raise the possibility that multi-locus CSD *might* explain the absence of diploid males from clonal lines other than clonal line A (as one of several alternative possibilities).

Overall, these are relatively minor points in the context of a strong manuscript, but I believe addressing them would improve the clarity and robustness of the authors' conclusions.

Reviewer #3 (Public review):

Summary:

The sex determination mechanism governed by the complementary sex determination (CSD) locus is one of the mechanisms that support the haplodiploid sex determination system evolved in hymenopteran insects. While many ant species are believed to possess a CSD locus, it has only been specifically identified in two species. The authors analyzed diploid females and the rarely occurring diploid males of the clonal ant Ooceraea biroi and identified a 46 kb CSD candidate region that is consistently heterozygous in females and predominantly homozygous in males. This region was found to be homologous to the CSD locus reported in distantly related ants. In the Argentine ant, Linepithema humile, the CSD locus overlaps with an lncRNA (ANTSR) that is essential for female development and is associated with the heterozygous region (Pan et al. 2024). Similarly, an lncRNA is encoded near the heterozygous region within the CSD candidate region of O. biroi. Although this lncRNA shares low sequence similarity with ANTSR, its potential functional involvement in sex determination is suggested. Based on these findings, the authors propose that the heterozygous region and the adjacent lncRNA in O. biroi may trigger female development via a mechanism similar to that of L. humile. They further suggest that the molecular mechanisms of sex determination involving the CSD locus in ants have been highly conserved for approximately 112 million years. This study is one of the few to identify a CSD candidate region in ants and is particularly noteworthy as the first to do so in a parthenogenetic species.

Strengths:

(1) The CSD candidate region was found to be homologous to the CSD locus reported in distantly related ant species, enhancing the significance of the findings.

(2) Identifying the CSD candidate region in a parthenogenetic species like O. biroi is a notable achievement and adds novelty to the research.

Weaknesses

(1) Functional validation of the lncRNA's role is lacking, and further investigation through knockout or knockdown experiments is necessary to confirm its involvement in sex determination.

See response below.

(2) The claim that the lncRNA is essential for female development appears to reiterate findings already proposed by Pan et al. (2024), which may reduce the novelty of the study.

We do not claim that the lncRNA is essential for female development in O. biroi, but simply mention the possibility that, as in L. humile, it is somehow involved in sex determination. We do not have any functional evidence for this, so this is purely based on its genomic position immediately adjacent to our mapped candidate region. We agree with the reviewer that the study by Pan et al. (2024) decreases the novelty of our findings. Another way of looking at this is that our study supports and bolsters previous findings by partially replicating the results in a different species.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

L307-308 should state homozygous for either allele in THE MAJORITY of diploid males.

This will be fixed in the revised manuscript, in what will be line 321.

Reviewer #3 (Recommendations for the authors):

The association between heterozygosity in the CSD candidate region and female development in O. biroi, along with the high sequence homology of this region to CSD loci identified in two distantly related ant species, is not sufficient to fully address the evolution of the CSD locus and the mechanisms of sex determination.

Given that functional genetic tools, such as genome editing, have already been established in O. biroi, I strongly recommend that the authors investigate the role of the lncRNA through knockout or knockdown experiments and assess its impact on the sex-specific splicing pattern of the downstream tra gene.

Although knockout experiments of the lncRNA would be illuminating, the primary signal of complementary sex determination is heterozygosity. As is clearly stated in our manuscript and that of (Pan et al. 2024), it does not appear to be heterozygosity within the lncRNA that induces female development, but rather heterozygosity in non-transcribed regions linked to the lncRNA. Therefore, future mechanistic studies of sex determination in O. biroi, L. humile, and other ants should explore how homozygosity or heterozygosity of this region impacts the sex determination cascade, rather than focusing (exclusively) on the lncRNA.

With this in mind, we developed three sets of guide RNAs that cut only one allele within the mapped CSD locus, with the goal of producing deletions within the highly variable region within the mapped locus. This would lead to functional hemizygosity or homozygosity within this region, depending on how the cuts were repaired. We also developed several sets of PCR primers to assess the heterozygosity of the resultant animals. After injecting 1,162 eggs over several weeks and genotyping the hundreds of resultant animals with PCR, we confirmed that we could induce hemizygosity or homozygosity within this region, at least in ~1/20 of the injected embryos. Although it is possible to assess the sex-specificity of the splice isoform of tra as a proxy for sex determination phenotypes (as done by (Pan et al. 2024)), the ideal experiment would assess male phenotypic development at the pupal stage. Therefore, over several more weeks, we injected hundreds more eggs with these reagents and reared the injected embryos to the pupal stage. However, substantial mortality was observed, with only 12 injected eggs developing to the pupal stage. All of these were female, and none of them had been successfully mutated.

In conclusion, we agree with the reviewer that functional experiments would be useful, and we made extensive attempts to conduct such experiments. However, these experiments turned out to be extremely challenging with the currently available protocols. Ultimately, we therefore decided to abandon these attempts.  

We opted not to include these experiments in the paper itself because we cannot meaningfully interpret their results. However, we are pleased that, in this response letter, we can include a brief description for readers interested in attempting similar experiments.

Since O. biroi reproduces parthenogenetically and most offspring develop into females, observing a shift from female- to male-specific splicing of tra upon early embryonic knockout of the lncRNA would provide much stronger evidence that this lncRNA is essential for female development. Without such functional validation, the authors' claim (lines 36-38) seems to reiterate findings already proposed by Pan et al. (2024) and, as such, lacks sufficient novelty.

We have responded to the issue of “lack of novelty” above. But again, the actual CSD locus in both O. biroi and L. humile appears to be distinct from (but genetically linked to) the lncRNA, and we have no experimental evidence that the putative lncRNA in O. biroi is involved in sex determination at all. Because of this, and given the experimental challenges described above, we do not currently intend to pursue functional studies of the lncRNA.

References

Hasselmann M, Gempe T, Schiøtt M, Nunes-Silva CG, Otte M, Beye M. 2008. Evidence for the evolutionary nascence of a novel sex determination pathway in honeybees. Nature 454:519–522.

Koch V, Nissen I, Schmitt BD, Beye M. 2014. Independent Evolutionary Origin of fem Paralogous Genes and Complementary Sex Determination in Hymenopteran Insects. PLOS ONE 9:e91883.

Matthey-Doret C, van der Kooi CJ, Jeffries DL, Bast J, Dennis AB, Vorburger C, Schwander T. 2019. Mapping of multiple complementary sex determination loci in a parasitoid wasp. Genome Biology and Evolution 11:2954–2962.

Miyakawa MO, Mikheyev AS. 2015. QTL mapping of sex determination loci supports an ancient pathway in ants and honey bees. PLOS Genetics 11:e1005656.

Pan Q, Darras H, Keller L. 2024. LncRNA gene ANTSR coordinates complementary sex determination in the Argentine ant. Science Advances 10:eadp1532.

Privman E, Wurm Y, Keller L. 2013. Duplication and concerted evolution in a master sex determiner under balancing selection. Proceedings of the Royal Society B: Biological Sciences 280:20122968.

Rabeling C, Kronauer DJC. 2012. Thelytokous parthenogenesis in eusocial Hymenoptera. Annual Review of Entomology 58:273–292.

Schmieder S, Colinet D, Poirié M. 2012. Tracing back the nascence of a new sex-determination pathway to the ancestor of bees and ants. Nature Communications 3:1–7.

Vorburger C. 2013. Thelytoky and Sex Determination in the Hymenoptera: Mutual Constraints. Sexual Development 8:50–58.

Author response:

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

Reviewer #1 (Public review):

Summary:

Dendrotweaks provides its users with a solid tool to implement, visualize, tune, validate, understand, and reduce single-neuron models that incorporate complex dendritic arbors with differential distribution of biophysical mechanisms. The visualization of dendritic segments and biophysical mechanisms therein provide users with an intuitive way to understand and appreciate dendritic physiology.

Strengths:

(1) The visualization tools are simplified, elegant, and intuitive.

(2) The ability to build single-neuron models using simple and intuitive interfaces.

(3) The ability to validate models with different measurements.

(4) The ability to systematically and progressively reduce morphologically-realistic neuronal models.

Weaknesses:

(1) Inability to account for neuron-to-neuron variability in structural, biophysical, and physiological properties in the model-building and validation processes.

We agree with the reviewer that it is important to account for neuron-to-neuron variability. The core approach of DendroTweaks, and its strongest aspect, is the interactive exploration of how morpho-electric parameters affect neuronal activity. In light of this, variability can be achieved through the interactive updating of the model parameters with widgets. In a sense, by adjusting a widget (e.g., channel distribution or kinetics), a user ends up with a new instance of a cell in the parameter space and receives almost real-time feedback on how this change affected neuronal activity. This approach is much simpler than implementing complex optimization protocols for different parameter sets, which would detract from the interactivity aspect of the GUI. In its revised version, DendroTweaks also accounts for neuron-to-neuron morphological variability, as channel distributions are now based on morphological domains (rather than the previous segment-specific approach). This makes it possible to apply the same biophysical configuration across various morphologies. Overall, both biophysical and morphological variability can be explored within DendroTweaks. 

(2) Inability to account for the many-to-many mapping between ion channels and physiological outcomes. Reliance on hand-tuning provides a single biased model that does not respect pronounced neuron-to-neuron variability observed in electrophysiological measurements.

We acknowledge the challenge of accounting for degeneracy in the relation between ion channels and physiological outcomes and the importance of capturing neuron-to-neuron variability. One possible way to address this, as we mention in the Discussion, is to integrate automated parameter optimization algorithms alongside the existing interactive hand-tuning with widgets. In its revised version, DendroTweaks can integrate with Jaxley (Deistler et al., 2024) in addition to NEURON. The models created in DendroTweaks can now be run with Jaxley (although not all types of models, see the limitations in the Discussion), and their parameters can be optimized via automated and fast gradient-based parameter optimization, including optimization of heterogeneous channel distributions. In particular, a key advantage of integrating Jaxley with DendroTweaks was its NMODL-to-Python converter, which significantly reduced the need to manually re-implement existing ion channel models for Jaxley (see here: https://dendrotweaks.readthedocs.io/en/latest/tutorials/convert_to_jaxley.html).

(1) Michael Deistler, Kyra L. Kadhim, Matthijs Pals, Jonas Beck, Ziwei Huang, Manuel Gloeckler, Janne K. Lappalainen, Cornelius Schröder, Philipp Berens, Pedro J. Gonçalves, Jakob H. Macke Differentiable simulation enables large-scale training of detailed biophysical models of neural dynamics bioRxiv 2024.08.21.608979; doi:https://doi.org/10.1101/2024.08.21.608979

Lack of a demonstration on how to connect reduced models into a network within the toolbox.

Building a network of reduced models is an exciting direction, yet beyond the scope of this manuscript, whose primary goal is to introduce DendroTweaks and highlight its capabilities. DendroTweaks is designed for single-cell modeling, aiming to cover its various aspects in great detail. Of course, we expect refined single-cell models, both detailed and simplified, to be further integrated into networks. But this does not need to occur within DendroTweaks. We believe this network-building step is best handled by dedicated network simulation platforms. To facilitate the network-building process, we extended the exporting capabilities of DendroTweaks. To enable the export of reduced models in DendroTweaks’s modular format, as well as in plain simulator code, we implemented a method to fit the resulting parameter distributions to analytical functions (e.g., polynomials). This approach provided a compact representation, requiring a few coefficients to be stored in order to reproduce a distribution, independently of the original segmentation. The reduced morphologies can be exported as SWC files, standardized ion channel models as MOD files, and channel distributions as JSON files. Moreover, plain NEURON code (Python) to instantiate a cell class can be automatically generated for any model, including the reduced ones. Finally, to demonstrate how these exported models can be integrated into larger simulations, we implemented a "toy" network model in a Jupyter notebook included as an example in the GitHub repository. We believe that these changes greatly facilitate the integration of DendroTweaks-produced models into networks while also allowing users to run these networks on their favorite platforms.

(4) Lack of a set of tutorials, which is common across many "Tools and Resources" papers, that would be helpful in users getting acquainted with the toolbox.

This is an important point that we believe has been addressed fully in the revised version of the tool and manuscript. As previously mentioned, the lack of documentation was due to the software's early stage. We have now added comprehensive documentation, which is available at https://dendrotweaks.readthedocs.io. This extensive material includes API references, 12 tutorials, 4 interactive Jupyter notebooks, and a series of video tutorials, and it is regularly updated with new content. Moreover, the toolbox's GUI with example models is available through our online platform at https://dendrotweaks.dendrites.gr.  

Reviewer #2 (Public review):

The paper by Makarov et al. describes the software tool called DendroTweaks, intended for the examination of multi-compartmental biophysically detailed neuron models. It offers extensive capabilities for working with very complex distributed biophysical neuronal models and should be a useful addition to the growing ecosystem of tools for neuronal modeling.

Strengths

(1) This Python-based tool allows for visualization of a neuronal model's compartments.

(2) The tool works with morphology reconstructions in the widely used .swc and .asc formats.

(3) It can support many neuronal models using the NMODL language, which is widely used for neuronal modeling.

(4) It permits one to plot the properties of linear and non-linear conductances in every compartment of a neuronal model, facilitating examination of the model's details.

(5) DendroTweaks supports manipulation of the model parameters and morphological details, which is important for the exploration of the relations of the model composition and parameters with its electrophysiological activity.

(6) The paper is very well written - everything is clear, and the capabilities of the tool are described and illustrated with great attention to detail.

Weaknesses

(1) Not a really big weakness, but it would be really helpful if the authors showed how the performance of their tool scales. This can be done for an increasing number of compartments - how long does it take to carry out typical procedures in DendroTweaks, on a given hardware, for a cell model with 100 compartments, 200, 300, and so on? This information will be quite useful to understand the applicability of the software.

DendroTweaks functions as a layer on top of a simulator. As a result, its performance scales in the same way as for a given simulator. The GUI currently displays the time taken to run a simulation (e.g., in NEURON) at the bottom of the Simulation tab in the left menu. While Bokeh-related processing and rendering also consume time, this is not as straightforward to measure. It is worth noting, however, that this time is short and approximately equivalent to rendering the corresponding plots elsewhere (e.g., in a Jupyter notebook), and thus adds negligible overhead to the total simulation time. 

(2) Let me also add here a few suggestions (not weaknesses, but something that can be useful, and if the authors can easily add some of these for publication, that would strongly increase the value of the paper).

(3) It would be very helpful to add functionality to read major formats in the field, such as NeuroML and SONATA.

We agree with the reviewer that support for major formats will substantially improve the toolbox, ensuring the reproducibility and reusability of the models. While integration with these formats has not been fully implemented, we have taken several steps to ensure elegant and reproducible model representation. Specifically, we have increased the modularity of model components and developed a custom compact data format tailored to single-cell modeling needs. We used a JSON representation inspired by the Allen Cell Types Database schema, modified to account for non-constant distributions of the model parameters. We have transitioned from a representation of parameter distributions dependent on specific segmentation graphs and sections to a more generalized domain-based distribution approach. In this revised methodology, segment groups are no longer explicitly defined by segment identifiers, but rather by specification of anatomical domains and conditional expressions (e.g., “select all segments in the apical domain with the maximum diameter < 0.8 µm”). Additionally, we have implemented the export of experimental protocols into CSV and JSON files, where the JSON files contain information about the stimuli (e.g., synaptic conductance, time constants), and the CSV files store locations of recording sites and stimuli. These features contribute toward a higher-level, structured representation of models, which we view as an important step toward eventual compatibility with standard formats such as NeuroML and SONATA. We have also initiated a two-way integration between DendroTweaks and SONATA. We developed a converter from DendroTweaks to SONATA that automatically generates SONATA files to reproduce models created in DendroTweaks. Additionally, support for the DendroTweaks JSON representation of biophysical properties will be added to the SONATA data format ecosystem, enabling models with complex dendritic distributions of channels. This integration is still in progress and will be included in the next version of DendroTweaks. While full integration with these formats is a goal for future releases, we believe the current enhancements to modularity and exportability represent a significant step forward, providing immediate value to the community.

(4) Visualization is available as a static 2D projection of the cell's morphology. It would be nice to implement 3D interactive visualization.

We offer an option to rotate a cell around the Y axis using a slider under the plot. This is a workaround, as implementing a true 3D visualization in Bokeh would require custom Bokeh elements, along with external JavaScript libraries. It's worth noting that there are already specialized tools available for 3D morphology visualization. In light of this, while a 3D approach is technically feasible, we advocate for a different method. The core idea of DendroTweaks’ morphology exploration is that each section is “clickable”, allowing its geometric properties to be examined in a 2D "Section" view. Furthermore, we believe the "Graph" view presents the overall cell topology and distribution of channels and synapses more clearly.

(5) It is nice that DendroTweaks can modify the models, such as revising the radii of the morphological segments or ionic conductances. It would be really useful then to have the functionality for writing the resulting models into files for subsequent reuse.

This functionality is fully available in local installations. Users can export JSON files with channel distributions and SWC files after morphology reduction through the GUI. Please note that for resource management purposes, file import/export is disabled on the public online demo. However, it can be enabled upon local installation by modifying the configuration file (app/default_config.json). In addition, it is now possible to generate plain NEURON (Python) code to reproduce a given model outside the toolbox (e.g., for network simulations). Moreover, it is now possible to export the simulation protocols as CSV files for locations of stimuli and recordings and JSON files for stimuli parameters.

(6) If I didn't miss something, it seems that DendroTweaks supports the allocation of groups of synapses, where all synapses in a group receive the same type of Poisson spike train. It would be very useful to provide more flexibility. One option is to leverage the SONATA format, which has ample functionality for specifying such diverse inputs.

Currently, each population of “virtual” neurons that form synapses on the detailed cell shares the same set of parameters for both biophysical properties of synapses (e.g., reversal potential, time constants) and presynaptic "population" activity (e.g., rate, onset). The parameter that controls an incoming Poisson spike train is the rate, which is indeed shared across all synapses in a population. Unfortunately, the current implementation lacks the capability to simulate complex synaptic inputs with heterogeneous parameters across individual synapses or those following non-uniform statistical distributions (the present implementation is limited to random uniform distributions). We have added this information in the Discussion (3. Discussion - 3.2 Limitations and future directions - ¶.5) to make users aware of the limitations. As it requires a substantial amount of additional work, we plan to address such limitations in future versions of the toolbox.

(7) "Each session can be saved as a .json file and reuploaded when needed" - do these files contain the whole history of the session or the exact snapshot of what is visualized when the file is saved? If the latter, which variables are saved, and which are not? Please clarify.

In the previous implementation, these files captured the exact snapshot of the model's latest state. In the new version, we adopted a modular approach where the biophysical configuration (e.g., channel distributions) and stimulation protocols are exported to separate files. This allows the user to easily load and switch the stimulation protocols for a given model. In addition, the distribution of parameters (e.g., channel conductances) is now based on the morphological domains and is agnostic of the exact morphology (i.e., sections and segments), which allows the same JSON files with biophysical configurations to be reused across multiple similar morphologies. This also allows for easy file exchange between the GUI and the standalone version.

Joint recommendations to Authors:

The reviewers agreed that the paper is well written and that DendroTweaks offers a useful collection of tools to explore models of single-cell biophysics. However, the tooling as provided with this submission has critical limitations in the capabilities, accessibility, and documentation that significantly limit the utility of DendroTweaks. While we recognize that it is under active development and features may have changed already, we can only evaluate the code and documentation available to us here.

We thank the reviewers for their positive evaluation of the manuscript and express our sincere appreciation for their feedback. We acknowledge the limitations they have pointed out and have addressed most of these concerns in our revised version.

In particular, we would emphasize:

(1) While the features may be rich, the documentation for either a user of the graphical interface or the library is extremely sparse. A collection of specific tutorials walking a GUI user through simple and complex model examples would be vital for genuine uptake. As one category of the intended user is likely to be new to computational modeling, it would be particularly good if this documentation could also highlight known issues that can arise from the naive use of computational techniques. Similarly, the library aspect needs to be documented in a more standard manner, with docstrings, an API function list, and more didactic tutorials for standard use cases.

DendroTweaks now features comprehensive documentation. The standalone Python library code is well-documented with thorough docstrings. The overall code modularity and readability have improved. The documentation is created using the widely adopted Sphinx generator, making it accessible for external contributors, and it is available via ReadTheDocs https://dendrotweaks.readthedocs.io/en/latest/index.html. The documentation provides a comprehensive set of tutorials (6 basic, 6 advanced) covering all key concepts and workflows offered by the toolbox. Interactive Jupyter notebooks are included in the documentation, along with the quick start guide. All example models also have corresponding notebooks that allow users to build the model from scratch.

The toolbox has its own online platform, where a quick-start guide for the GUI is available https://dendrotweaks.dendrites.gr/guide.html. We have created video tutorials for the GUI covering the basic use cases. Additionally, we have added tips and instructions alongside widgets in the GUI, as well as a status panel that displays application status, warnings, and other information. Finally, we plan to familiarize the community with the toolbox by organizing online and in-person tutorials, as the one recently held at the CNS*2025 conference (https://cns2025florence.sched.com/event/25kVa/building-intuitive-and-efficient-biophysicalmodels-with-jaxley-and-dendrotweaks). Moreover, the toolbox was already successfully used for training young researchers during the Taiwan NeuroAI 2025 Summer School, founded by Ching-Lung Hsu. The feedback was very positive.

(2) The paper describes both a GUI web app and a Python library. However, the code currently mixes these two in a way that largely makes sense for the web app but makes it very difficult to use the library aspect. Refactoring the code to separate apps and libraries would be important for anyone to use the library as well as allowing others to host their own DendroTweak servers. Please see the notes from the reviewing editor below for more details.

The code in the previous `app/model` folder, responsible for the core functionality of the toolbox, has been extensively refactored and extended, and separated into a standalone library. The library is included in the Python package index (PyPI, https://pypi.org/project/dendrotweaks).

Notes from the Reviewing Editor Comments (Recommendations for the authors):

(1) While one could import morphologies and use a collection of ion channel models, details of synapse groups and stimulation approaches appeared to be only configurable manually in the GUI. The ability to save and load full neuron and simulation states would be extremely useful for reproducibility and sharing data with collaborators or as an interactive data product with a publication. There is a line in the text about saving states as json files (also mentioned by Reviewer #2), but I could see no such feature in the version currently online.

We decided to reserve the online version for demonstration and educational purposes, with more example models being added over time. However, this functionality is available upon local installation of the app (and after specifying it in the ‘default_config.json’ in the root directory of the app). We’ve adopted a modular model representation to store separately morphology, channel models, biophysical parameters, and stimulation protocols.

(2) Relatedly, GUI exploration of complex data is often a precursor to a more automated simulation run. An easy mechanism to go from a user configuration to scripting would be useful to allow the early strength of GUIs to feed into the power of large-scale scripting.

Any model could be easily exported to a modular DendroTweaks representation and later imported either in the GUI or in the standalone version programmatically. This ensures a seamless transition between the two use cases.

(3) While the paper discusses DendroTweaks as both a GUI and a python library, the zip file of code in the submission is not in good form as a library. Back-end library code is intermingled with front-end web app code, which limits the ability to install the library from a standard python interface like PyPI. API documentation is also lacking. Functions tend to not have docstrings, and the few that do, do not follow typical patterns describing parameters and types.

As stated above, all these issues have been resolved in the new version of the toolbox. The library code is now housed in a separate repository https://github.com/Poirazi-Lab/DendroTweaks and included in PyPI https://pypi.org/project/dendrotweaks. The classes and public methods follow Numpy-style docstrings, and the API reference is available in the documentation: https://dendrotweaks.readthedocs.io/en/latest/genindex.html.

(4) Library installation is very difficult. The requirements are currently a lockfile, fully specifying exact versions of all dependencies. This is exactly correct for web app deployment to maintain consistency, but is not feasible in the context of libraries where you want to have minimal impact on a user's environment. Refactoring the library from the web app is critical for making DendroTweaks usable in both forms described in the paper.

The lockfile makes installation more or less impossible on computer setups other than that of the author. Needless to say, this is not acceptable for a tool, and I would encourage the authors to ask other people to attempt to install their code as they describe in the text. For example, attempting to create a conda environment from the environment.yml file on an M1 MacBook Pro failed because it could not find several requirements. I was able to get it to install within a Linux docker image with the x86 platform specified, but this is not generally viable. To make this be the tool it is described as in text, this must be resolved. A common pattern that would work well here is to have a requirements lockfile and Docker image for the web app that imports a separate, more minimally restrictive library package with that could be hosted on PyPI or, less conveniently, through conda-forge.

The installation of the standalone library is now straightforward via pip install dendrotweaks.On the Windows platform, however, manual installation of NEURON is required as described          in the official NEURON documentation https://nrn.readthedocs.io/en/8.2.6/install/install_instructions.html#windows.

(5) As an aside, to improve potential uptake, the authors might consider an MIT-style license rather than the GNU Public License unless they feel strongly about the GPL. Many organizations are hesitant to build on GPL software because of the wide-ranging demands it places on software derived from or using GPL code.

We thank the editor for this suggestion. We are considering changing the licence to MPL 2.0. It will maintain copyleft restrictions only on the package files while allowing end-users to freely choose their own license for any derived work, including the models, generated data files, and code that simply imports and uses our package.

Reviewer #1 (Recommendations for the authors):

(1) Abstract: Neurons rely on the interplay between dendritic morphology and ion channels to transform synaptic inputs into a sequence of somatic spikes. Technically, this would have to be morphology, ion channels, pumps, transporters, exchangers, buffers, calcium stores, and other molecules. For instance, if the calcium buffer concentration is large, then there would be less free calcium for activating the calcium-activated potassium channels. If there are different chloride co-transporters - NKCC vs. KCC - expressed in the neuron or different parts of the neuron, that would alter the chloride reversal for all the voltage- or ligand-gated chloride channels in the neuron. So, while morphology and ion channels are two important parts of the transformation, it would be incorrect to ignore the other components that contribute to the transformation. The statement might be revised to make these two components as two critical components.

The phrase “Two critical components” was added as it was suggested by the reviewer.

(2) Section 2.1 - The overall GUI looks intuitive and simple.

(3) Section 2.2

(a) The Graph view of morphology, especially accounting for the specific d_lambda is useful.

(b) "Note that while microgeometry might not significantly affect the simulation at a low spatial resolution (small number of segments) due to averaging, it can introduce unexpected cell behavior at a higher level of spatial discretization."

It might be good to warn the users that the compartmentalization and error analyses are with reference to the electrical lambda. If users have to account for calcium microdomains, these analyses wouldn't hold given the 2 orders of magnitude differences between the electrical and the calcium lambdas (e.g., Zador and Koch, J Neuroscience, 1994). Please sensitize users that the impact of active dendrites in regulating calcium microdomains and signaling is critical when it comes to plasticity models in morphologically realistic structures.

We thank the reviewer for this important point. We have clarified in the text that our spatial discretization specifically refers to the electrical length constant. We acknowledge that electrical and chemical processes operate on fundamentally different spatial and temporal scales, which requires special consideration when modeling phenomena like synaptic plasticity. We have sensitized users about this distinction. However, we do not address such examples in the manuscript, thus leaving the detailed discussion of non-electrical compartmentalization beyond the scope of this work.

(c) I am not very sure if the "smooth" tool for diameters that is illustrated is useful. Users shouldn't consider real variability in morphology as artifacts of reconstruction. As mentioned above, while this might not be an issue with electrical compartmentalization, calcium compartmentalization will severely be affected by small changes in morphology. Any model that incorporates calcium-gated channels should appropriately compartmentalize calcium. Without this, the spread of activation of calcium-dependent conductances would be an overestimate. Even small changes in cellular shape and curvature can have large impacts when it comes to signaling in terms of protein aggregation and clustering.

Although this functionality is still available in the toolbox, we have removed the emphasis from it in the manuscript. Nevertheless, for the purpose of addressing the reviewer’s comment, we provide an example when this “smoothening” might be needed:please see Figure S1 from Tasciotti et al. 2025.

(2) Simone Tasciotti, Daniel Maxim Iascone, Spyridon Chavlis, Luke Hammond, Yardena Katz, Attila Losonczy, Franck Polleux, Panayiota Poirazi. From Morphology to Computation: How Synaptic Organization Shapes Place Fields in CA1 Pyramidal Neurons bioRxiv 2025.05.30.657022; doi: https://doi.org/10.1101/2025.05.30.657022

(4) Section 2.3

(a) The graphical representation of channel gating kinetics is very useful.

(b) Please warn the users that experimental measurements of channel gating kinetics are extremely variable. Taking the average of the sigmoids or the activation/deactivation/inactivation kinetics provides an illusion that each channel subtype in a given cell type has fixed values of V_1/2, k, delta, and tau, but it is really a range obtained from several experiments. The heterogeneity is real and reflects cell-to-cell variability in channel gating kinetics, not experimental artifacts. Please sensitize the readers that there is not a single value for these channel parameters.

This is a fair comment, and it refers to a general problem in neuronal modeling. In DendroTweaks, we follow the approach widely used in the community that indeed doesn't account for heterogeneity. We added a paragraph in the revised manuscript's Discussion (3. Discussion - 3.3 Limitations and future directions - ¶.3) to address this issue.

(5) Section 2.4

(a) Same as above: Please sensitize users that the gradients in channel conductances are measured as an average of measurements from several different cells. This gradient need not be present in each neuron, as there could be variability in location-dependent measurements across cells. The average following a sigmoid doesn't necessarily mean that each neuron will have the channel distributed with that specific sigmoid (or even a sigmoid!) with the specific parametric values that the average reported. This is extremely important because there is an illusion that the gradient is fixed across cells and follows a fixed functional form.

We added this information to our Discussion in the same paragraph mentioned above.

(b) Please provide an example where the half-maximal voltage of a channel varies as a function of distance (such as Poolos et al., Nature Neuroscience, 2002 or Migliore et al., 1999; Colbert and Johnston, 1997). This might require a step-like function in some scenarios. An illustration would be appropriate because people tend to assume that channel gating kinetics are similar throughout the dendrite. Again, please mention that these shifts are gleaned from the average and don't really imply that each neuron must have that specific gradient, given neuron-to-neuron variability in these measurements.

We thank the reviewer for the provided literature, which we now cite when describing parameter distributions (2. Results - 2.4 Distributing ion channels - ¶.1). Please note that DendroTweaks' programming interface and data format natively support non-linear distribution of kinetic parameters alongside the channel conductances. As for the step-like function, users can either directly apply the built-in step-like distribution function or create it by combining two constant distributions.

(6) Section 2.5

(a) It might be useful to provide a mechanism for implementing the normalization of unitary conductances at the cell body, (as in Magee and Cook, 2000; Andrasfalvy et al., J Neuroscience, 2001). Specifically, users should be able to compute AMPAR conductance values at each segment which would provide a somatic EPSP value of 0.2 mV.

This functionality is indeed useful and will be added in future releases. Currently, it has been mentioned in the list of known limitations when working with synaptic inputs (3. Discussion - 3.3 Limitations and future directions - ¶.5).

(b) Users could be sensitized about differences in decay time constants of GABA_A receptors that are associated with parvalbamin vs. somatostatin neurons. As these have been linked to slow and fast gamma oscillations and different somatodendritic locations along different cell types, this might be useful (e.g., 10.1016/j.neuron.2017.11.033;10.1523/jneurosci.0261-20.2020; 10.7554/eLife.95562.1; 10.3389/fncel.2023.1146278).

We thank the reviewer for highlighting this important biological detail. DendroTweaks enables users to define model parameters specific to their cell type of interest. For practical reasons, we leave the selection of biologically relevant parameters to the users. However, we will consider adding an explicit example in our tutorials to showcase the toolbox's flexibility in this regard.

(7) Section 2.6

While reducing the morphological complexity has its advantages, users of this tool should be sensitized in this section about how the reduction does not capture all the complexity of the dendritic computation. For instance, the segregation/amplification properties of Polsky et al., 2004, Larkum et al., 2009 would not be captured by a fully reduced model. An example across different levels of reductions, implementing simulations in Figure 7F (but for synapses on the same vs. different branches), would be ideal. Demonstrate segregation/amplification in the full model for the same set of synapses - coming on the same branch/different branch (linear integration of synapses on different branches and nonlinear integration of synapses on the same branch). Then, show that with different levels of reduction, this segregation/amplification vanishes in the reduced model. In addition, while impedance-based approaches account for account for electrical computation, calcium-based computation is not something that is accountable with reduced models, given the small lambda_calcium values. Given the importance of calcium-activated conductances in electrical behaviour, this becomes extremely important to account for and sensitize users to. The lack of such sensitization results in presumptuous reductions that assume that all dendritic computation is accounted for by reduced models!

We agree with the reviewer that reduction leads to a loss in the complexity of dendritic computation. This has been stated in both the original algorithm paper (Amsalem et al., 2020) and in our manuscript (e.g., 3. Discussion - 3.2 Comparison to existing modeling software - ¶.6). In fact, to address this problem, we extended the functionality of neuron_reduce to allow for multiple levels of morphology reduction. Our motivation for integrating morphology reduction in the toolbox was to leverage the exploratory power of DendroTweaks to assess how different degrees of reduction alter cell integrative properties, determining which computations are preserved, which are lost, and at what specific reduction level these changes occur. Nevertheless, to address this comment, we've made it more explicit in the Discussion that reduction inevitably alters integrative properties and, at a certain level, leads to loss of dendritic computations.

(8) Section 2.7

(a) The validation process has two implicit assumptions:

(i) There is only one value of physiological measurements that neurons and dendrites are endowed with. The heterogeneity in these measurements even within the same cell type is ignored. The users should be allowed to validate each measurement over a range rather than a single value. Users should be sensitized about the heterogeneity of physiological measurements.

(ii) The validation process is largely akin to hand-tuning models where a one-to-one mapping of channels to measurements is assumed. For instance, input resistance can be altered by passive properties, by Ih, and by any channel that is active under resting conditions. Firing rate and patterns can be changed by pretty much every single ion channel that expresses along the somatodendritic axis.

An updated validation process that respects physiological heterogeneities in measurements and accounts for global dependencies would be more appropriate. Please update these to account for heterogeneities and many-to-many mappings between channels and measurements. An ideal implementation would be to incorporate randomized search procedures (across channel parameters spanning neuron-to-neuron variability in channel conductances/gating properties) to find a population of models that satisfy all physiological constraints (including neuron-to-neuron variability in each physiological measurement), rather than reliance on procedures that are akin to hand-tuning models. Such population-based approaches are now common across morphologically-realistic models for different cell types (e.g., Rathour and Narayanan, PNAS, 2014; Basak and Narayanan, J Physiology, 2018; Migliore et al., PLoS Computational Biology, 2018; Basak and Narayanan, Brain Structure and Function, 2020; Roy and Narayanan, Neural Networks, 2021; Roy and Narayanan, J Physiology, 2023; Arnaudon et al., iScience, 2023; Reva et al., Patterns, 2023; Kumari and Narayanan, J Neurophysiology, 2024) and do away with the biases introduced by hand-tuning as well as the assumption of one-to-one mapping between channels and measurements.

We appreciate the reviewer’s comment and the suggested alternatives to our validation process. We have extended the discussion on these alternative approaches (3. Discussion - 2. Comparison to existing modeling software - ¶.5). However, it is important to note that neither one-value nor one-to-one mapping assumption is imposed in our approach. It is true that validation is performed on a given model instance with fixed single-value parameters. However, users can discover heterogeneity and degeneracy in their models via interactive exploration. In the GUI, a given parameter can be changed, and the influence of this change on model output can be observed in real time. Validation can be run after each change to see whether the model output still falls within a biologically plausible regime or not. This is, of course, time-consuming and less efficient than any automated parameter optimization.

However, and importantly, this is the niche of DendroTweaks. The approach we provide here can indeed be referred to as model hand-tuning. This is intentional: we aim to complement black-box optimization by exposing the relationship between parameters and model outputs. DendroTweaks is not aimed at automated parameter optimization and is not meant to provide the user with parameter ranges automatically. The built-in validation in DendroTweaks is intended as a lightweight, fast feedback tool to guide manual tuning of dendritic model parameters so as to enhance intuitive understanding and assess the plausibility of outputs, not as a substitute for comprehensive model validation or optimization. The latter can be done using existing frameworks, designed for this purpose, as mentioned by the reviewer. 

(b) Users could be asked to wait for RMP to reach steady state. For instance, in some of the traces in Figure 7, the current injection is provided before RMP reaches steady-state. In the presence of slow channels (HCN or calcium-activated channels), the RMP can take a while to settle down. Users might be sensitized about this. This would also bring to attention the ability of several resting channels in modulating RMP, and the need to wait for steady-state before measurements are made.

We agree with the observation and updated the validation process accordingly. We have added functionality for simulation stabilization, allowing users to pre-run a simulation before the main simulation time. For example, model.run(duration=1000, prerun_time=300) could be used to stabilize the model for a period of 300 ms before running the main simulation for 1 s.

(c) Strictly speaking, it is incorrect to obtain membrane time constant by fitting a single exponential to the initial part of the sag response (Figure 7A). This may be confirmed in the model by setting HCN to zero (strictly all active channel conductances to zero), obtaining the voltage-response to a pulse current, fitting a double exponential (as Rall showed, for a finite cable or for a real neuron, a single exponential would yield incorrect values for the tau) to the voltage response, and mapping membrane time constant to the slower of the two time-constants (in the double exponential fit). This value will be very different from what is obtained in Figure 7A. Please correct this, with references to Rall's original papers and to electrophysiological papers that use this process to assess membrane properties of neurons and their dendrites (e.g., Stuart and Spruston, J Neurosci, 1998; Golding and Spruston, J Physiology, 2005).

We updated the algorithm for calculating the membrane time constant based on the reviewer's suggestions and added the suggested references. The time constant is now obtained in a model with blocked HCN channels (setting maximal conductance to 0) via a double exponential fit, taking the slowest component.

(9) Section 3

(a) May be good to emphasize the many-to-many mapping between ion channels and neuronal functions here in detail, and on how to explore this within the Dendrotweaks framework.

We have added a paragraph in the Discussion that addresses both the problems of heterogeneity and degeneracy in biological neurons and neuronal models (3. Discussion - 3.3 Limitations and future directions - ¶.3)

(b) May be good to have a specific section either here or in results about how the different reduced models can actually be incorporated towards building a network.

As mentioned earlier, building a network of reduced models is a promising new direction. However, it is beyond the scope of this manuscript, whose primary goal is to introduce DendroTweaks and highlight its capabilities. DendroTweaks is designed for single-cell modeling and provides export capabilities that allow integrating it into broader workflows, including network modeling. We have added a paragraph in the manuscript (3. Discussion - 3.1 Conceptual and implementational accessibility - ¶.2) that addresses how DendroTweaks could be used alongside other software, in particular for scaling up single-cell models to the network level.

(10) Section 4

(a) Section 4.3: In the second sentence (line 568), the "first Kirchhoff's law" within parentheses immediately after Q=CV gives an illusion that Q=CV is the first Kirchhoff's law! Please state that this is with reference to the algebraic sum of currents at a node.

We have corrected the equations and apologize for this oversight. 

(b) Table 1: In the presence of active ion channels, input resistance, membrane time constant, and voltage attenuation are not passive properties. Input resistance is affected by any active channel that is active at rest (HCN, Kir, A-type K+ through the window current, etc). The same holds for membrane time constant and voltage attenuation as well. This could be made clear by stating if these measurements are obtained in the presence or absence of active ion channels. In real neurons, all these measurements are affected by active ion channels; so, ideally, these are also active properties, not passive! Also, please mention that in the presence of resonating channels (e.g., HCN, M-type K+), a single exponential fit won't be appropriate to obtain tau, given the presence of sag.

We thank the reviewer for pointing out this ambiguity. What the term “Passive” means in Table 1 (e.g., for the input resistance, R_in) is that the minimal set of parameters needed to validate R_in are the passive ones (i.e., Cm, Ra, and Leak). We have changed the table listing to reflect this.

Reviewer #2 (Recommendations for the authors):

(1) Figure 2B and the caption to Figure 2F show and describe the diameter of the sections, whereas the image in Figure 2F shows the radius. Which is the correct one?

The reason for this is that Figure 2B shows the sections' geometry as it is represented in NEURON, i.e., with diameters, while Figure 2F shows the geometry as it is represented in an SWC file (as these changes are made based on the SWC file). Nevertheless, as mentioned earlier, we decided to remove panel F from the figure in the new version, to present a more important panel on tree graph representations.

(2) "Each segment can be viewed as an equivalent RC circuit representing a part of the membrane". The example in Figure 2B is perhaps a relatively simple case. For more complex cases where multiple nonlinear conductances are present in each section, would it be possible to show each of these conductances explicitly? If yes, it would be nice to illustrate that.

We would like to clarify that "can be viewed" here was intended to mean "can be considered," and we have updated the text accordingly. The schematic RC circuits were added to the corresponding figure for illustration purposes only and are not present in the GUI, as this would indeed be impractical for multiple conductances.

(3) Some extra citations could be added. For example, it is a little strange that BRIAN2 is mentioned, but NEST is not. It might be worth mentioning and citing it. Also, the Allen Cell Types Database is mentioned, but no citation for it is given. It could be useful to add such citations (https://doi.org/10.1038/s41593-019-0417-0, https://doi.org/10.1038/s41467-017-02718-3).

Brian 2 is extensively used in our lab on its own and as a foundation of the Dendrify library (Pagkalos et al., 2023). As stated in the discussion, we are considering bridging reduced Hodgkin-Huxley-type models to Dendrify leaky integrate-and-fire type models. For these reasons, Brian 2 is mentioned in the discussion. However, we acknowledge that our previous overview omitted references to some key software, which have now been added to the updated manuscript. We appreciate the reviewer providing references that we had overlooked.

(3) Pagkalos, M., Chavlis, S. & Poirazi, P. Introducing the Dendrify framework for incorporating dendrites to spiking neural networks. Nat Commun 14, 131 (2023). https://doi.org/10.1038/s41467-022-35747-8

Author response:

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

Reviewer #1 (Public Review):

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

After validating the viral strategy and the specificity of the targeting (immunochemistry and electrophysiology), the authors demonstrate that while both NAc Shell D1- and D2SPNs participate in mediating sPIT, NAc Shell D1-SPNs projections to the Ventral Pallidum (VP, previously demonstrated as crucial for sPIT), but not D2-SPNs, mediates sPIT. They also show that these eNects were specific to stimulus-based actions, as valuebased choices were left intact in all manipulations. 

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

We thank the Reviewer for their positive assessment. 

Reviewer 2 (Public Review):

Summary: 

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

Strengths: 

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

We thank the Reviewer for their positive assessment. 

Weaknesses: 

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

We acknowledge the reviewer's valuable suggestion that demonstrating NAc-S D1- and D2-SPNs engagement in outcome-specific PIT through another technique would strengthen our optogenetic findings. Several approaches could provide this validation. Chemogenetic manipulation, as the reviewer suggested, represents one compelling option. Alternatively, immunohistochemical assessment of phosphorylated histone H3 at serine 10 (P-H3) oMers another promising avenue, given its established utility in reporting striatal SPNs plasticity in the dorsal striatum (Matamales et al., 2020). We hope to complete such an assessment in future work since it would address the limitations of previous work that relied solely on ERK1/2 phosphorylation measures in NAc-S SPNs (Laurent et al., 2014). The manuscript was modified to report these future avenues of research (page 12). 

Regarding the null result from optical silencing of D2 terminals in the ventral pallidum, we agree with the reviewer's assessment. While we acknowledge this limitation in the current manuscript (page 13), we aim to address this gap in future studies to provide a more complete mechanistic understanding of the circuit.

Reviewer 3 (Public Review):

Summary:

The authors present data demonstrating that optogenetic inhibition of either D1- or D2MSNs in the NAc Shell attenuates expression of sensory-specific PIT while largely sparing value-based decision on an instrumental task. They also provide evidence that SS-PIT depends on D1-MSN projections from the NAc-Shell to the VP, whereas projections from D2-MSNs to the VP do not contribute to SS-PIT.

Strengths:

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

We thank the Reviewer for their positive assessment. 

Weaknesses:

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

We appreciate the reviewer's comment regarding the marginal attenuation of valuebased choice observed following NAc-S D1-SPN silencing. While this manipulation did produce a slight reduction in choice performance, the behavior remained largely intact. We are hesitant to interpret this marginal eMect as evidence for a direct role of NAc-S D1SPNs in value-based decision-making, particularly given the substantial literature demonstrating that NAc-S manipulations typically preserve such choice behavior (Corbit et al., 2001; Corbit & Balleine, 2011; Laurent et al., 2012). Furthermore, previous work has shown that NAc-S D1 receptor blockade impairs outcome-specific PIT while leaving value-based choice unaMected (Laurent et al., 2014). We favor an alternative explanation for our observed marginal reduction. As documented in Supplemental Figure 1, viral transduction extended slightly into the nucleus accumbens core (NAc-C), a region established as critical for value-based decision-making (Corbit et al., 2001; Corbit & Balleine, 2011; Laurent et al., 2012; Parkes et al., 2015). The marginal impairment may therefore reflect inadvertent silencing of a small number of  NAc-C D1-SPNs rather than a functional contribution from NAc-S D1-SPNs. Future studies specifically targeting larger NAc-C D1-SPN populations would help clarify this possibility and provide definitive resolution of this question.

Reviewer 1 (Recommendations for the Author):

My main concerns and comments are listed below.

(1) Could the authors provide the "raw" data of the PIT tests, such as PreSame vs Same vs PreDiNerent vs DiNerent? Could the authors clarify how the Net responding was calculated? Was it Same minus PreSame & DiNerent minus PreDiNerent, or was the average of PreSame and PreDiNerent used in this calculation?

The raw data for PIT testing across all experiments are now included in the Supplemental Figures (Supplemental Figures S1E, S2E, S3E, and S4E). Baseline responding was quantified as the average number of lever presses per minute for both actions during the two-minute period (i.e., average of PreSame and PreDiMerent) preceding each stimulus presentation. This methodology has been clarified in the revised manuscript (page 7).

(2) While both sexes are utilized in the current study, no statistical analysis is provided. Can the authors please comment on this point and provide these analyses (for both training and tests)?

As noted in the original manuscript, the final sample sizes for female and male rats were insuMicient to provide adequate statistical power for sex-based analyses (page 15). To address this limitation, we have now cited a previous study from our laboratory (Burton et al., 2014) that conducted such analyses with suMicient power in identical behavioural tasks. That study identified only marginal sex diMerences in performance, with female rats exhibiting slightly higher magazine entry rates during Pavlovian conditioning. Importantly, no diMerences were observed in outcome-specific PIT or value-based choice performance between sexes.

(3) Regarding Figure 1 - Anterograde tracing in D1-Cre and A2a-Cre rats (from line 976), I have one major and one minor question:

(3.1) I do not understand the rationale of showing anterograde tracing from the Dorsal Striatum (DS) as this region is not studied in the current work. Moreover, sagittal micrographs of D1-Cre and A2a-Cre would be relevant here. Could the authors please provide these micrographs and explain the rationale for doing tracing in DS?

We included dorsal striatum (DS) tracing data as a reference because the projection patterns of D1 and D2 SPNs in this region are well-established and extensively characterized, in contrast to the more limited literature on these cell types in the NAc-S. Regarding the comment about sagittal micrographs, we are uncertain of the specific concern as these images are presented in Figure 1B.

If the reviewer is requesting sagittal micrographs for NAc-S anterograde tracing, we did not employ this approach because: (1) the NAc-S and ventral pallidum are anatomically adjacent regions and (2) the medial-lateral coordinates of the ventral pallidum and lateral hypothalamus do not align optimally with those of the NAc-S, limiting the utility of sagittal analysis for these projections.

(3.2) There is no description about how the quantifications were done: manually? Automatically? What script or plugin was used? If automated, what were the thresholding conditions? How many brain sections along the anteroposterior axis? What was the density of these subpopulations? Can the authors include a methodological section to address this point?

We apologize for the omission of quantification methods used to assess viral transduction specificity. This methodological description has now been added to the revised manuscript (page 22). Briefly, we employed a manual procedure in two sections per rat, and cell counts were completed in a defined region of interest located around the viral infusion site.

(4) Lex A & Hauber (2008) Dopamine D1 and D2 receptors in the nucleus accumbens core and shell mediate Pavlovian-instrumental transfer. Learning & memory 15:483- 491, should be cited and discussed. It also seems that the contribution of the main dopaminergic source of the brain, the ventral tegmental area, is not cited, while it has been investigated in PIT in at least 3 studies regarding sPIT only, notably the VP-VTA pathway (Leung & Balleine 2015, accurately cited already).

We did not include the Lex & Hauber (2008) study because its experimental design (single lever and single outcome) prevents diMerentiation between the eMects of Pavlovian stimuli on action performance (general PIT) versus action selection (outcome-specific PIT, as examined in the present study). Drawing connections between their findings and our results would require speculative interpretations regarding whether their observed eMects reflect general or outcome-specific PIT mechanisms, which could distract from the core findings reported in the article.

Several studies examining the role of the VTA in outcome-specific PIT were referenced in the manuscript's introduction. Following the reviewer's recommendation, these references have also been incorporated into the discussion section (page 13). 

(5) While not directly the focus of this study, it would be interesting to highlight the accumbens dissociation between General vs Specific PIT, and how the dopaminergic system (diNerentially?) influences both forms of PIT.

We agree with the reviewer that the double dissociation between nucleus accumbens core/shell function and general/specific PIT is an interesting topic. However, the present manuscript does not examine this dissociation, the nucleus accumbens core, or general PIT. Similarly, our study does not directly investigate the dopaminergic system per se. We believe that discussing these topics would distract from our core findings and substantially increase manuscript length without contributing novel data directly relevant to these areas. 

(6) While authors indicate that conditioned response to auditory stimuli (magazine visits) are persevered in all groups, suggesting intact sensitivity to the general motivational properties of reward-predictive stimuli (lines 344, 360), authors can't conclude about the specificity of this behavior i.e. does the subject use a mental representation of O1 when experiencing S1, leading to a magazine visits to retrieve O1 (and same for S2-O2), or not? Two food ports would be needed to address this question; also, authors should comment on the fact that competition between instrumental & pavlovian responses does not explain the deficits observed.

We agree with the Reviewer that magazine entry data cannot be used to draw conclusions about specificity, and we do not make such claims in our manuscript. We are therefore unclear about the specific concern being raised. Following the Reviewer’s recommendation, we have commented on the fact that response competition could not explain the results obtained (page 11, see also supplemental discussion). 

The minor comments are listed below.

(7) A high number of rats were excluded (> 32 total), and the number of rats excluded for NAc-S D1-SPNs-VP is not indicated.

We apologize for omitting the number of rats excluded from the experiment examining NAc-S D1-SPN projections to the ventral pallidum. This information has been added to the revised manuscript (page 22).

(7.1) Can authors please comment on the elevated number of exclusions?

A total of 133 rats were used across the reported experiments, with 40 rats excluded based on post-mortem analyses. This represents an attrition rate of approximately 30%, which we consider reasonable given that most animals received two separate viral infusions and two separate fiber-optic cannula implantations, and that the inclusion of both female and male rats contributed to some variability in coordinates and so targeting. 

(7.2) Can authors please present the performance of these animals during the tasks (OFF conditions, and for control ones, both ON & OFF conditions)?

Rats were excluded after assessing the spread of viral infusions, placement of fibre-optic cannulas and potential damage due to the surgical procedures (page 21). The requested data are presented below and plotted in the same manner as in Figures 3-6. The pattern of performance in excluded animals was highly variable. 

Author response image 1.

(8) For tracing, only males were used, and for electrophysiology, only females were used.

(8.1) Can authors please comment on not using both sexes in these experiments? 

We agree that equal allocation of female and male rats in the experiments presented in Figures 1-2 would have been preferable. Animal availability was the sole factor determining these allocations. Importantly, both female and male D1-Cre and A2A-Cre rats were used for the NAc-S tracing studies, and no sex diMerences were observed in the projection patterns. The article describing the two transgenic lines of rats did not report any sex diMerence (Pettibone et al., 2019). 

(8.2) Is there evidence in the literature that the electrophysiological properties of female versus male SPNs could diNer?

The literature indicates that there is no sex diMerence in the electrophysiological properties of NAc-S SPNs (Cao et al., 2018; Willett et al., 2016).  

(8.3) It seems like there is a discrepancy between the number of animals used as presented in the Figure 2 legend versus what is described in the main text. In the Figure legend, I understand that 5 animals were used for D1-Cre/DIO-eNpHR3.0 validation, and 7 animals for A2a-Cre/DIO-eNpHR3.0; however, the main text indicates the use of a total of 8 animals instead of the 12 presented in the Figure legend. Can authors please address this mismatch or clarify?

The number of rats reported in the main text and Figure 2 legend was correct. However, recordings sometimes involved multiple cells from the same animal, and this aspect of the data was incorrectly reported and generated confusion. We have clarified the numbers in both the main text and Figure 2 legend to distinguish between animal counts and cell counts. 

(9) Overall, in the study, have the authors checked for outliers?

Performance across all training and testing stages was inspected to identify potential behavioral outliers in each experiment. Abnormal performance during a single session within a multi-session stage was not considered suMicient grounds for outlier designation. Based on these criteria, no subjects remaining after post-mortem analyses exhibited performance patterns warranting exclusion through statistical outlier analysis. However, we have conducted the specific analyses requested by the Reviewer, as described below. 

(9.1) In Figure 3, it seems that one female in the eYFP group, in the OFF situation, for the diNerent condition, has a higher level of responding than the others. Can authors please confirm or refute this visual observation with the appropriate statistical analysis?

Statistical analysis (z-score) confirmed the reviewer's observation regarding responding of the diMerent action in the OFF condition for this subject (|z| = 2.58). Similar extreme responding was observed in the ON condition (|z| = 2.03). Analyzing responding on the diMerent action in isolation is not informative in the context of outcome-specific PIT. Additional analyses revealed |z| < 2 when examining the magnitude of choice discrimination in outcome-specific PIT (i.e., net same versus net diMerent responding) in both ON and OFF conditions. Furthermore, this subject showed |z| < 2 across all other experimental stages. Based on these analyses, we conclude that the subject should be kept in all analyses. 

(9.2) In Figure 5, it seems that one male, in the ON situation, in the diNerent condition, has a quite higher level of responding - is this subject an outlier? If so, how does it aNect the statistical analysis after being removed? And who is this subject in the OFF condition?

The reviewer has identified two diMerent male rats infused with the eNpHR3.0 virus and has asked closer examination of their performance.

The first rat showed outlier-level responding on the diMerent action in the ON condition (|z| = 2.89) but normal responding for all other measures across LED conditions (|z| < 2). Additional analyses revealed |z| = 2.55 when examining choice discrimination magnitude in outcome-specific PIT during the ON condition but not during the OFF condition (|z| = 0.62). This subject exhibited |z| < 2 across all other experimental stages.

The second rat showed outlier-level responding on the same action in the OFF condition (|z| = 2.02) but normal responding for all other measures across LED conditions (|z| < 2). Additional analyses revealed |z| = 2.12 when examining choice discrimination magnitude in outcome-specific PIT during the OFF condition but not during the ON condition (|z| = 0.67). This subject also exhibited |z| < 2 across all other experimental stages.

We excluded these two subjects and conducted the same analyses as described in the original manuscript. Baseline responding did not diMer between groups (p = 0.14), allowing to look at the net eMect of the stimuli. Overall lever presses were greater in the eYFP rats (Group: F(1,16) = 6.08, p < 0.05; η² = 0.28) and were reduced by LED activation (LED: F(1,16) = 9.52, p < 0.01; η² = 0.44) and this reduction depended on the group considered (Group x LED: F(1,16) = 12.125, p < 0.001; η² = 0.43). Lever press rates were higher on the action earning the same outcome as the stimuli compared to the action earning the diMerent outcome (Lever: F(1,16)= 49.32; η² = 0.76; p < 0.001), regardless of group (Group x Lever: p = 0.14). There was a Lever by LED light condition interaction (Lever x LED: F(1,16)= 5.25; η² = 0.24; p < 0.05) but no an interaction between group, LED light condition, and Lever during the presentation of the predictive stimuli (p = 0.10). Given the significant Group x LED and Lever x LED interactions, additional analyses were conducted to determine the source of these interactions. In eYFP rats, LED activation had no eMect (LED: p = 0.70) and lever presses were greater on the same action (Lever: (F(1,9) = 23.94, p < 0.001; η² = 0.79) regardless of LED condition (LED x Lever: p = 0.72). By contrast, in eNpHR3.0 rats, lever presses were reduced by LED activation (LED: F(1,9) = 23.97, p < 0.001; η² = 0.73), were greater on the same action (Lever: F(1,9) = 16.920, p < 0.001; η² = 0.65) and the two factors interacted (LED x Lever: F(1,9) = 9.12, p < 0.01; η² = 0.50). These rats demonstrated outcome-specific PIT in the OFF condition (F(1,9) = 27.26, p < 0.001; η² = 0.75) but not in the ON condition (p = 0.08).

Overall, excluding these two rats altered the statistical analyses, but both the original and revised analyses yielded the same outcome: silencing the NAc-S D1-SPN to VP pathway disrupted PIT. More importantly, we do not believe there are suMicient grounds to exclude the two rats identified by the reviewer. These animals did not display outlier-level responding across training stages or during the choice test. Their potential classification as outliers would be based on responding during only one LED condition and not the other, with notably opposite patterns between the two rats despite belonging to the same experimental group. 

(10) I think it would be appreciable if in the cartoons from Figure 5.A and 6.A, the SPNs neurons were color-coded as in the results (test plots) and the supplementary figures (histological color-coding), such as D1- in blue & D2-SPNs in red.

Our current color-coding system uses blue for D1-SPNs transduced with eNpHR3.0 and red for D2-SPNs transduced with eNpHR3.0. The D1-SPNs and D2-SPNs shown in Figures 5A and 6A represent cells transduced with either eYFP (control) or eNpHR3.0 virus and therefore cannot be assigned the blue or red color, which is reserved for eNpHR3.0transduced cells specifically. The micrographs in the Supplemental Figures maintain consistency with the color-coding established in the main figures.

(11) As there are (relatively small) variations in the control performance in term of Net responding (from ~3 to ~7 responses per min), I wonder what would be the result of pooling eYFP groups from the two first experiments (Figures 3 & 4) and from the two last ones (Figures 5 & 6) - would the same statically results stand or vary (as eYFP vs D1-Cre vs A2a-Cre rats)? In particular for Figures 3 & 4, with and without the potential outlier, if it's indeed an outlier.

We considered the Reviewer’s recommendation but do not believe the requested analysis is appropriate. The Reviewer is requesting the pooling of data from subjects of distinct transgenic strains (D1-Cre and A2A-Cre rats) that underwent surgical and behavioral procedures at diMerent time points, sometimes months apart. Each experiment was designed with necessary controls to enable adequate statistical analyses for testing our specific hypotheses. 

(12) Presence of cameras in operant cages is mentioned in methods, but no data is presented regarding recordings, though authors mention that they allow for real-time observations of behavior. I suggest removing "to record" or adding a statement about the fact that no videos were recorded or used in the present study.

We have removed “to record” from the manuscript (page 18). 

(13) In all supplementary Figures, "F" is wrongly indicated as "E".

We thank the Reviewer for reporting these errors, which have been corrected. 

(14) While the authors acknowledge that the eNicacy of optogenetic inhibition of terminals is questionable, I think that more details are required to address this point in the discussion (existing literature?). Maybe, the combination of an anterograde tracer from SPNs to VP, to label VP neurons (to facilitate patching these neurons), and the Credependent inhibitory opsin in the NAc Shell, with optogenetic illumination at the level of the VP, along with electrophysiological recordings of VP neurons, could help address this question but may, reasonably, seem challenging technically.

Our manuscript does not state that optogenetic inhibition of terminals is questionable. It acknowledges that we do not provide any evidence about the eMicacy of the approach. Regardless, we have provided additional details and suggestions to address this lack of evidence (page 13). 

(15) A nice addition could be an illustration of the proposed model (from line 374), but it may be unnecessary.

We have carefully considered the reviewer's recommendation. The proposed model is detailed in three published articles, including one that is freely accessible, which we have cited when presenting the model in our manuscript (page 14). This reference should provide interested readers with easy access to a comprehensive illustration of the model.

Reviewer 2 (Recommendations for the Author):

As noted in my public comments, this is a truly excellent and compelling study. I have only a few minor comments.

(1) I could not find the coordinates/parameters for the dorsal striatal AAV injections for that component of the tract tracing experiment.

We apologize for this omission, which has now been corrected (page 16). 

(2) Please add the final group sizes to the figure captions.

We followed the Reviewer’s recommendation and added group sizes in the main figure captions. 

(3) The discussion of group exclusions (p 21 line 637) seems to accidentally omit (n = X) the number of NAc-S D1-SPNs-VP mice excluded.

We apologize for this omission, which has now been corrected (page 22). 

(4) There were some labeling issues in the supplementary figures (perhaps elsewhere, too). Specifically, panel E was listed twice (once for F) in captions.

We apologize for this error, which has now been corrected.  

(5) Inspection of the magazine entry data from PIT tests suggests that the optogenetic manipulations may have had some eNects on this behavior and would encourage the authors to probe further. There was a significant group diNerence for D1-SPN inhibition and a marginal group eNect for D2-SPNs. The fact that these eNects were in opposite directions is intriguing, although not easily interpreted based on the canonical D1/D2 model. Of course, the eNects are not specific to the light-on trials, but this could be due to carryover into light-oN trials. An analysis of trial-order eNects seems crucial for interpreting these eNects. One might also consider normalizing for pre-test baseline performance. Response rates during Pavlovian conditioning seem to suggest that D2eNpHR mice showed slightly higher conditioned responding during training, which contrasts with their low entry rates at test. I don't see any of this as problematic -- but more should be done to interpret these findings.

We thank the reviewer for raising this interesting point regarding magazine entry rates. Since these data are presented in the Supplemental Figures, we have added a section in the Supplemental Material file that elaborates on these findings. This section does not address trial order eMects, as trial order was fully counterbalanced in our experiments and the relevant statistical analyses would lack adequate power. Baseline normalization was not conducted because the reviewer's suggestion was based on their assumption that eNpHR3.0 rats in the D2-SPNs experiment showed slightly higher magazine entries during Pavlovian training. However, this was not the case. In fact, like the eNpHR3.0 rats in the D1-SPNs experiment, they tended to display lower magazine entries during training. The added section therefore focuses on the potential role of response competition during outcome-specific PIT tests. Although we concluded that response competition cannot explain our findings, we believe it may complicate interpretation of magazine entry behavior. Thus, we recommend that future studies examine the role of NAc-S SPNs using purely Pavlovian tasks. It is worth nothing that we have recently completed experiments (unpublished) examining NAc-S D1- and D2-SPN silencing during stimulus presentation in a Pavlovian task identical to the one used here. Silencing of either SPN population had no eMect on magazine entry behavior.

Reviewer 3 (Recommendations for the Author):

Broad comments:

Throughout the manuscript, the authors draw parallels between the eNect established via pharmacological manipulations and those shown here with optogenetic manipulation. I understand using the pharmacological data to launch this investigation, but these two procedures address very diNerent physiological questions. In the case of a pharmacological manipulation, the targets are receptors, wherever they are expressed, and in the case of D2 receptors, this means altering function in both pre-synaptically expressed autoreceptors and post-synaptically expressed D2 MSN receptors. In the case of an optogenetic approach, the target is a specific cell population with a high degree of temporal control. So I would just caution against comparing results from these types of studies too closely.

Related to this point is the consideration of the physiological relevance of the manipulation. Under normal conditions, dopamine acts at D1-like receptors to increase the probability of cell firing via Ga signaling. In contrast, dopamine binding of D2-like receptors decreases the cell's firing probability (signaling via Gi/o). Thus, shunting D1MSN activation provides a clear impression of the role of these cells and, putatively, the role of dopamine acting on these cells. However, inhibiting D2-MSNs more closely mimics these cells' response to dopamine (though optogenetic manipulations are likely far more impactful than Gi signaling). All this is to say that when we consider the results presented here in Experiment 2, it might suggest that during PIT testing, normal performance may require a halting of DA release onto D2-MSNs. This is highly speculative, of course, just a thought worth considering.

We agree with the comments made by the Reviewer, and the original manuscript included statements acknowledging that pharmacological approaches are limited in the capacity to inform about the function of NAc-S SPNs (pages 4 and 9). As noted by the Reviewer, these limitations are especially salient when considering NAc-S D2-SPNs. Based on the Reviewer’s comment, we have modified our discussion to further underscore these limitations (page 12). Finally, we agree with the suggestion that PIT may require a halting of DA release onto D2-SPNs. This is consistent with the model presented, whereby D2-SPNs function is required to trigger enkephalin release (page 13).     

Section-Specific Comments and Questions:

Results:

Anterograde tracing and ex vivo cell recordings in D1 Cre and A2a Cre rats: Why are there no statistics reported for the e-phys data in this section? Was this merely a qualitative demonstration? I realize that the A2a-Cre condition only shows 3 recordings, so I appreciate the limitations in analyzing the data presented.

The reviewer is correct that we initially intended to provide a qualitative demonstration. However, we have now included statistical analyses for the ex vivo recordings. It is important to note that there were at least 5 recordings per condition, though overlapping data points may give the impression of fewer recordings in certain conditions. We have provided the exact number of recordings in both the main text (page 5) and figure legend. 

What does trial by trial analysis look like, because in addition to the eNects of extinction, do you know if the responsiveness of the opsin to light stimulation is altered after repeated exposures, or whether the cells themselves become compromised in any way with repeated light-inhibition, particularly given the relatively long 2m duration of the trial.

The Reviewer raises an interesting point, and we provide complete trial-by-trial data for each experiment below. As identified by the Reviewer, there is some evidence for extinction, although it remained modest. Importantly, the data suggest that light stimulation did not aMect the physiology of the targeted cells. In eNpHR3.0 rats, performance across OFF trials remained stable (both for Same and DiMerent) even though they were preceded by ON trials, indicating no carryover eMects from optical stimulation.

Author response image 2.

The statistics for the choice test are not reported for eNpHR-D1-Cre rats, but do show a weakening of the instrumental devaluation eNect "Group x Lever x LED: F1,18 = 10.04, p < 0.01, = 0.36". The post hoc comparisons showed that all groups showed devaluation, but it is evident that there is a weakening of this eNect when the LED was on (η² = 0.41) vs oN (η² = 0.78), so I think the authors should soften the claim that NAcS-D1s are not involved in value-based decision-making. (Also, there is a typo in the legend in Figure S1, where the caption for panel "F" is listed as "E".) I also think that this could be potentially interesting in light of the fact that with circuit manipulation, this same weakening of the instrumental devaluation eNect was not observed. To me, this suggests that D1-NAcS that project to a diNerent region (not VP) contribute to value-based decision making.

This comment overlaps with one made in the Public Review, for which we have already provided a response. Given its importance, we have added a section addressing this point in the supplemental discussion of the Supplementary Material file, which aligns with the location of the relevant data. The caption labelling error has been corrected.

Materials and Methods:

Subjects:

Were these heterozygous or homozygous rats? If hetero, what rats were used for crossbreeding (sex, strain, and vendor)? Was genotyping done by the lab or outsourced to commercial services? If genotyping was done within the lab, please provide a brief description of the protocol used. How was food restriction established and maintained (i.e., how many days to bring weights down, and was maintenance achieved by rationing or by limiting ad lib access to food for some period in the day)?

The information requested by the Reviewer have been added to the subjects section (pages 15-16).  

Were rats pair/group housed after implantation of optic fibers?

We have clarified that rats were group houses throughout (see subjects section; pages 15-16). 

Behavioral Procedures:

How long did each 0.2ml sucrose infusion take? For pellets, for each US delivery, was it a single pellet or two in quick succession?

We have modified the method section to indicate that the sucrose was delivered across 2 seconds and that a single pellet was provided (page 17). 

The CS to ITI duration ratio is quite low. Is there a reason such a short ratio was used in training?

These parameters are those used in all our previous experiments on outcome-specific PIT. There is no specific reason for using such a ratio, except that it shortens the length of the training session. 

Relative to the end of training, when were the optical implantation surgeries conducted, and how much recovery time was given before initiating reminder training and testing?

Fibre-optic implantation was conducted 3-4 days after training and another 3-4 days were given for recovery. This has been clarified in the Materials and methods section (pages 15-16).

I think a diagram or schematic showing the timeline for surgeries, training, and testing would be helpful to the audience.

We opted for a text-based experimental timeline rather than a diagram due to slight temporal variations across experiments (page 15).

On trials, when the LED was on, was light delivered continuously or pulsed? Do these opto-receptors 'bleach' within such a long window?

We apologize for the lack of clarity; the light was delivered continuously. We have modified the manuscript (pages 6 and 19) and figure legend accordingly. The postmortem analysis did not provide evidence for photobleaching (Supplemental Figures) and as noted above, the behavioural results do not indicate any negative physiological impact on cell function.  

Immunofluorescence: The blocking solution used during IHC is described as "NHS"; is this normal horse serum?

The Reviewer is correct; NHS stands for normal horse serum. This has been added (page 21). 

Microscopy and imaging:

For the description of rats excluded due to placement or viral spread problems, an n=X is listed for the NAc S D1 SPNs --> VP silencing group. Is this a typo, or was that meant to read as n=0? Also, was there a major sex diNerence in the attrition rate? If so, I think reporting the sex of the lost subjects might be beneficial to the scientific community, as it might reflect a need for better guidance on sex-specific coordinates for targeting small nuclei.

We apologize for the error regarding the number of excluded animals. This error has been corrected (page 23). There were no major sex diMerences in the attrition rate. The manuscript has been updated to provide information about the sex of excluded animals (page 23). 

References

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Laurent, V., Bertran-Gonzalez, J., Chieng, B. C., & Balleine, B. W. (2014). δ-Opioid and Dopaminergic Processes in Accumbens Shell Modulate the Cholinergic Control of Predictive Learning and Choice. J Neurosci, 34(4), 1358-1369. https://doi.org/10.1523/JNEUROSCI.4592-13.2014

Laurent, V., Leung, B., Maidment, N., & Balleine, B. W. (2012). μ- and δ-opioid-related processes in the accumbens core and shell diMerentially mediate the influence of reward-guided and stimulus-guided decisions on choice. J Neurosci, 32(5), 1875-1883. https://doi.org/10.1523/JNEUROSCI.4688-11.2012

Matamales, M., McGovern, A. E., Mi, J. D., Mazzone, S. B., Balleine, B. W., & BertranGonzalez, J. (2020). Local D2- to D1-neuron transmodulation updates goal-directed learning in the striatum. Science, 367(6477), 549-555. https://doi.org/10.1126/science.aaz5751

Parkes, S. L., Bradfield, L. A., & Balleine, B. W. (2015). Interaction of insular cortex and ventral striatum mediates the eMect of incentive memory on choice between goaldirected actions. J Neurosci, 35(16), 6464-6471. https://doi.org/10.1523/JNEUROSCI.4153-14.2015

Pettibone, J. R., Yu, J. Y., Derman, R. C., Faust, T. W., Hughes, E. D., Filipiak, W. E., Saunders, T. L., Ferrario, C. R., & Berke, J. D. (2019). Knock-In Rat Lines with Cre Recombinase at the Dopamine D1 and Adenosine 2a Receptor Loci. eNeuro, 6(5). https://doi.org/10.1523/ENEURO.0163-19.2019

Willett, J. A., Will, T., Hauser, C. A., Dorris, D. M., Cao, J., & Meitzen, J. (2016). No Evidence for Sex DiMerences in the Electrophysiological Properties and Excitatory Synaptic Input onto Nucleus Accumbens Shell Medium Spiny Neurons. eNeuro, 3(1), ENEURO.0147-15.2016. https://doi.org/10.1523/ENEURO.0147-15.2016

Author response:

The following is the authors’ response to the original reviews

Public Reviews: 

Reviewer #1 (Public review): 

This study presents evidence that remote memory in the APP/PS1 mouse model of Alzheimer's disease (AD) is associated with PV interneuron hyperexcitability and increased inhibition of cortical engram cells. Its strength lies in the fact that it explores a neglected aspect of memory research - remote memory impairments related to AD (for which the primary research focus is usually on recent memory impairments) -which has received minimal attention to date. While the findings are intriguing, the weakness of the paper hovers around purely correlational types of evidence and superficial data analyses, which require substantial revisions as outlined below. 

We thank the reviewer for their feedback, and we appreciate the recognition of the study’s novelty in addressing remote memory impairments in AD. We acknowledge the reviewer’s concerns and have implemented revisions to strengthen the manuscript.

Major concerns: 

(1) In light of previous work, including that by the authors themselves, the data in Figure 1 should be implemented by measurements of recent memory recall in order to assess whether remote memories are exclusively impaired or whether remote memory recall merely represents a continuation of recent memory impairments.

We agree with the reviewer that is an important point. In line with their suggestion in minor comment 1, we now omitted the statement on recent memory in the results (previously on lines 109-111 and 117). Nonetheless, previous independent experiments from our group have repeatedly shown recent memory deficits in APP/PS1 mice at 12 weeks of age, including a recent article published in 2023. We refer the reviewer to figure 2c in Végh et al. (2014) and figure 2i in Kater et al. (2023). We have added a reference of the latter paper to our discussion section (line 458-459). Therefore, we are confident that the recent memory deficit at 12 weeks of age is a stable phenotype in our APP/PS1 mice.

With these data in mind, we argue that the remote memory recall impairment is not a continuation of recent memory impairments. Recent memory deficits emerge already at 12 weeks of age, and when remote memory is assessed at 16 weeks (4 weeks after training at 12 weeks of age), APP/PS1 mice are still capable of forming and retrieving a remote memory. This suggests that remote memory retrieval can occur even when recent memory is compromised, arguing against the idea that the remote memory deficit observed at 20 weeks is a continuation of earlier recent memory impairments. We have clarified this point in the revised manuscript by adding the following sentence to the discussion section (line 462-465): 

‘This suggests that a remote memory can be formed even when recent memory expression is already compromised, indicating that the remote memory deficit in 20-week-old APP/PS1 mice is not a continuation of earlier recent memory impairments.’

(2) Figure 2 shows electrophysiological properties of PV cells in the mPFC that correlate with the behavior shown in Figure 1. However, the mice used in Figure 2 are different than the mice used in Figure 1. Thus, the data are correlative at best, and the authors need to confirm that behavioral impairments in the APP/PS1 mice crossed to PV-Cre (and SST-Cre mice) used in Figure 2 are similar to those of the APP/PS1 mice used in Figure 1. Without that, no conclusions between behavioral impairments and electrophysiological as well as engram reactivation properties can be made, and the central claims of the paper cannot be upheld. 

We thank the reviewer for raising this concern. Indeed, the remote memory impairment and PV hyperexcitability are correlative data, and therefore we do not make causal claims based on these data. However, please note that most of our key findings, including behavioural impairments, characterization of the engram ensemble and reactivation thereof, as well as inhibitory input measurements, were acquired using the same mouse line (APP/PS1), strengthening the coherence of our conclusions. Also, our electrophysiological findings in APP/PS1 (enhanced sIPSC frequency) and APP/PS1-PV-Cre-tdTomato (enhanced PV cell excitability) mice align well. Direct comparisons between the transgenic mouse lines APP/PS1 and APP/PS1 Parv-Cre were performed in our previous studies, confirming that these lines are similar in terms of behaviour and pathology. Specifically, we demonstrated that APP/PS1 mice display spatial memory impairments at 16 weeks of age, Fig 4a-d, consistent with the deficits observed in APP/PS1 Parv-Cre mice at 16 weeks of age, Fig 5a-c (Hijazi et al., 2020a). Additionally, Hijazi et al. (2020a) showed that soluble and insoluble Aβ levels do not differ between APP/PS1 Parv-Cre and APP/PS1 mice (sFig. 1), indicating comparable levels of pathology between these lines. While we do not have a similar characterization of the APP/PS1 SST-Cre line, we should mention that we also did not observe excitability differences in SST cells. We now acknowledge the limitation in the revised discussion section (line 480-487), and stress that our electrophysiology and behavioural findings are correlative in nature:

‘Although the excitability measurements were performed in APP/PS1-PV-Cre-tdTomato mice, and not in the APP/PS1 parental line, we previously found that these transgenic mouse lines exhibit comparable amyloid pathology (both soluble and insoluble amyloid beta levels) as well as similar spatial memory deficits (Hijazi et al., 2020a; Kater et al., 2023). Thus, our observations indicate that the APP/PS1 PV-Cre-tdTomato and APP/PS1 lines are similar in terms of pathology and behaviour. Nonetheless, further work is needed to identify a causal link between PV cell hyperexcitability and remote memory impairment.’ 

(3) The reactivation data starting in Figure 3 should be analysed in much more depth: 

a) The authors restrict their analysis to intra-animal comparisons, but additional ones should be performed, such as inter-animal (WT vs APP/PS1) as well as inter-age (12-16w vs 16-20w). In doing so, reactivation data should be normalized to chance levels per animal, to account for differences in labelling efficiency - this is standard in the field (see original Tonegawa papers and for a reference). This could highlight differences in total reactivation that are already apparent, such as for instance in WT vs APP/PS1 at 20w (Figure 3o) and highlight a decrease in reactivation in AD mice at this age, contrary to what is stated in lines 213-214. 

We would like to thank the reviewer for the valuable input on the reactivation data in Figure 3. 

We agree with the reviewer and now depict the data as normalized to chance levels (Figure 3). The original figures are now supplemental (sFig. 5). The reactivation data normalized to chance are similar to the original results, i.e. no difference was observed in the reactivation of the mPFC engram ensemble between genotypes. The reviewer may have overlooked that we did perform inter-animal (WT vs. APP/PS1) comparisons, however these were not significantly different. We have made this clearer in the main text, lines 277, 288-289, 294-295 and 303-304. Moreover, the reviewer recommended including inter-age group comparisons, which have now been added to the supplemental figures (sFig. 6). No genotype-dependent differences were observed. While a main effect of age group did emerge, indicating that there is a potential increased overlap between Fos+ and mCherry+ in animals aged 16-20 weeks, we caution against overinterpreting this finding. These experimental groups were processed in separate cohorts, with viral injection and 4TM-induced tagging performed at different moments in time, which may have contributed to the observed differences in overlap. We have addressed this point in the revised discussion (line 612-617):

‘Furthermore, we also observed an increase in the amount overlap between Fos+ and mCherry+ engram cells when comparing the 12-16w and 16-20w age groups. This finding should be interpreted with caution, as the experimental groups were processed in separate cohorts, with viral injections and 4TM-induced tagging performed at different moments in time. This may have contributed to the observed differences between ages.’

b) Comparing the proportion of mcherry+ cells in PV- and PV+ is problematic, considering that the PV- population is not "pure" like the PV+, but rather likely to represent a mix of different pyramidal neurons (probably from several layers), other inhibitory neurons like SST and maybe even glial cells. Considering this, the statement on line 218 is misleading in saying that PVs are overrepresented. If anything, the same populations should be compared across ages or groups.  

We thank the reviewer for their insightful comment and agree that the PV- population of cells is likely more heterogenous than the PV+ population. However, we would like to clarify that all quantified cells were selected based on Nissl immunoreactivity, and to exclude non-neuronal cells, stringent thresholding was applied in the script that was used to identify Nissl+ cells. The threshold information has now been added to the methods section (line 758-760). Thus, although heterogenous, the analysed PV- population reflects a neuronal subset. In response to the reviewer’s suggestion, we have now included overlap measurements relative to chance levels (Figure 3). These analyses did not reveal differences with the original analyses, i.e., there are no genotype specific differences. We have also incorporated the suggested inter-age group comparisons (sFig. 6) and found no differences between age groups. In light of the raised concerns, we have removed the statement that PV cells were overrepresented in the engram ensemble.

c) A similar concern applies to the mcherry- population in Figure 4, which could represent different types of neurons that were never active, compared to the relatively homogeneous engram mcherry+ population. This could be elegantly fixed by restricting the comparison to mCherry+Fos+ vs mCherry+Fos- ensembles and could indicate engram reactivation-specific differences in perisomatic inhibition by PV cells. 

The comparison the reviewer suggests, comparing mCherry+Fos+ to mCherry+Fos- is indeed conceptually interesting and could provide more insight into engram reactivation and PV input. However, there are practical limitations to performing this analysis, as neurons in close proximity need to be compared in a pairwise manner to account for local variability in staining intensity. As shown in Figure 3c+k and Figure 4a+b, d+e, PV immunostaining intensity varies to a certain extend within a given image. While pairwise comparisons of neighbouring neurons were feasible when analysing mCherry+ and mCherry- cells, they are unfortunately not feasible for the mCherry+Fos+ vs. mCherry+Fos- comparison. The occurrence of spatially adjacent mCherry+Fos+ and mCherry+Fos- neurons is too sparse for a pairwise comparison. This analysis would therefore result in substantial under-sampling and limit the reliability of the analysis. Nonetheless, we agree with the reviewer that the mCherry- population may be more heterogenous than the mCherry+ population, despite the fact that PV+ neurons and that non-neuronal cells were excluded from both populations in the analyses. We therefore added a statement to the discussion to acknowledge this limitation (line 536-539): 

‘Although PV+ cells were not included in this analysis and we excluded non-neuronal cells based on the area of the Nissl stain, the mCherry- population was potentially more heterogenous than the mCherry+ population, which may have contributed to the differences we observed.’

(4) At several instances, there are some doubts about the statistical measures having been employed: 

a) In Figure 4f, it is unclear why a repeated measurement ANOVA was used as opposed to a regular ANOVA. 

b) In Supplementary Figure 2b, a Mann-Whitney test was used, supposedly because the data were not normally distributed. However, when looking at the individual data points, the data does seem to be normally distributed. Thus, the authors need to provide the test details as to how they measured the normalcy of distribution. 

a) Based on the pairwise comparison of neighbouring neurons within animals, the data in Figure 4f was analysed with a repeated measure ANOVA. 

b) We thank the author for their comment on Supplementary Figure 2b. The data is indeed normally distributed, and we have analysed it using a D’Agostino & Pearson test. We have corrected this in the supplemental figure. 

Minor concerns: 

(1) Line 117: The authors cite a recent memory impairment here, as shown by another paper. However, given the notorious difficulty in replicating behavioral findings, in particular in APP/PS1 mice (number of backcrossings, housing conditions, etc., might differ between laboratories), such a statement cannot be made. The authors should either show in their own hands that recent memory is indeed affected at 12 weeks of age, or they should omit this statement. 

We thank the reviewer for this thoughtful comment. As noted in our response to major concern (1), we have addressed this concern by providing additional information and clarification in the discussion (line 462-465) regarding the possibility that remote memory impairments are a continuation of recent memory impairments. As mentioned in our response, we have added a reference to a more recent study from our lab (Kater et al. (2023). These findings are consistent with the earlier report from our lab (Végh et al. (2014), underscoring the reproducibility of this phenotype across independent cohorts and time. Notably, the experiments in the 2023 and present study were performed using the same housing and experimental conditions. Nevertheless, in light of the reviewer’s suggestion, and to avoid overstatement or speculation, we have now omitted the sentence referring to recent memory impairments at 12 weeks of age from the results section.

(2) Pertaining to Figure 3, low-resolution images of the mPFC should be provided to assess the spread of injection and the overall degree of double-positive cells.  

We agree with the reviewer and have added images of the mPFC as a supplemental figure (sFig. 3) that show the spread of the injection. Unfortunately, it is not possible to visualize the overall degree of double-positive cells at a lower magnification (or low-resolution). Representative examples of colocalization are presented in Figure 3.

Reviewer #2 (Public review): 

This study presents a comprehensive investigation of remote memory deficits in the APP/PS1 mouse model of Alzheimer's disease. The authors convincingly show that these deficits emerge progressively and are paralleled by selective hyperexcitability of PV interneurons in the mPFC. Using viral-TRAP labeling and patch-clamp electrophysiology, they demonstrate that inhibitory input onto labeled engram cells is selectively increased in APP/PS1 mice, despite unaltered engram size or reactivation. These findings support the idea that alterations in inhibitory microcircuits may contribute to cognitive decline in AD. 

However, several aspects of the study merit further clarification. Most critically, the central paradox, i.e., increased inhibitory input without an apparent change in engram reactivation, remains unresolved. The authors propose possible mechanisms involving altered synchrony or impaired output of engram cells, but these hypotheses require further empirical support. Additionally, the study employs multiple crossed transgenic lines without reporting the progression of amyloid pathology in the mPFC, which is important for interpreting the relationship between circuit dysfunction and disease stage. Finally, the potential contribution of broader network dysfunction, such as spontaneous epileptiform activity reported in APP/PS1 mice, is also not addressed. 

We thank the reviewer for their evaluation and appreciate the positive assessment of our study’s contributing to understanding remote memory deficits and the dysfunction of inhibitory microcircuits in AD. We also acknowledge the relevant points raised and have revised the manuscript to clarify our interpretations. 

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors): 

(1) Line 68: What are "APP23xPS45" mice? This is most likely a typo.

This line is a previously reported double transgenic amyloid beta mouse model that was obtained by crossing APP23 (overexpressing human amyloid precursor protein with the Swedish double mutation at position 670/671) with PS45 (carrying a transgene for mutant Presenilin 1, G384A mutation) (Busche et al., 2008; Grienberger et al., 2012). 

(2) Line 148: The authors should also briefly describe in the main text that APP/PS1 x SST-Cre mice were generated and used here.  

We thank the reviewer for their comment and have added their suggestion to the main text (line 166-168):

‘To do this, APP/PS1 mice were crossed with SST-Cre mice to generate APP/PS1 SST-Cre mice. Following microinjection of AAV-hSyn::DIO-mCherry into the mPFC, recordings were obtained from SST neurons.’

(3) The discussion should be condensed because of redundancies on several occasions. For example, memory allocation is discussed starting on line 371, then again on line 392. This should be combined. Likewise, how the correlative nature of the findings about PV interneurons could be further functionally addressed is discussed on lines 413 and 454, and should be condensed into one paragraph. 

We thank the reviewer for this suggestion and have revised the discussion to remove the redundancies as proposed.  

Reviewer #2 (Recommendations for the authors): 

To strengthen the manuscript, the following points should be addressed: 

(1) Quantify amyloid pathology: It is essential to assess amyloid-β levels (soluble and insoluble) in the mPFC of APP/PS1-PV-Cre-tdTomato mice at the studied ages. This would help determine whether the observed circuitlevel changes track with disease progression as seen in canonical APP/PS1 models. 

We thank the reviewer for this valuable suggestion and agree that assessing Aβ levels in the mPFC is important to determine whether the observed circuit level alterations in APP/PS1 mice coincide with the progression of amyloid pathology. Therefore, we assessed the amyloid plaque load in the mPFC of APP/PS1 mice at 16 and 20 weeks of age (new supplemental figure sFig. 1) and observed no difference in plaque load between these two time points. This suggests that the increased excitability in the mPFC cannot be attributed to differences in plaque load (insoluble amyloid beta).

In line with this, we previously studied both soluble and insoluble Aβ levels in the CA1 and reported that there are no differences between 12 and 16 weeks of age (Kater et al., 2023), while PV cell hyperexcitability is present at 16 weeks of age (Hijazi et al., 2020a). From 24 weeks onwards, the level of amyloid beta increases. Similarly, Végh et al. (2014) showed using immunoblotting that monomeric and low molecular weight oligomeric forms of soluble Aβ are already present as early as 6 weeks of age and become more prominent at 24 weeks of age. Although the soluble Aβ measurements were performed in the hippocampus, we think these findings can be extrapolated to cortical regions, as the APP and PS1 mutations in APP/PS1 mice are driven by a prion promotor, which should induce consistent expression across brain regions. Data from other research groups support this hypothesis (Kim et al., 2015; Zhang et al., 2011). Thus, large regional differences in soluble Aβ are not expected. The temporal progression suggests that increasing levels of soluble amyloid beta might contribute to the emergence of PV cell hyperexcitability. We have added this point to the manuscript (line 585-591):

‘Since amyloid beta plaque load in the mPFC remains comparable between 16- and 20-week-old APP/PS1 mice, the observed increased excitability is unlikely the result of changes in insoluble amyloid beta levels. Previous data from our lab show that soluble amyloid beta is already present as early as 6 weeks of age and becomes more prominent at 24 weeks of age (Kater et al., 2023; Végh et al., 2014). The progressive increase in soluble amyloid beta levels may contribute to the emergence of PV cell hyperexcitability.’

Finally, we previously compared soluble and insoluble amyloid beta levels in APP/PS1 and APP/PS1 Parv Cre mice and show that these are similar (Hijazi et al., 2020a). While our current study shows the progression of amyloid beta accumulation in APP/PS1 mice, these mice also exhibit altered microcircuitry (enhanced sIPSC frequency on engram cells) at 20 weeks of age, the same age at which we observed PV cell hyperexcitability in APP/PS1 Parv Cre tdTomato mice. This further supports the generalizability of our findings across genotypes, between APP/PS1 and APP/PS1 Parv Cre tdTomato mice. 

(2) Examine later disease stages: Since the current effects are modest, assessing memory performance, PV cell excitability, and engram inhibition at more advanced stages could clarify whether these alterations become more pronounced with disease progression. 

We thank the reviewer for this thoughtful suggestion. Investigating advanced disease stages could indeed provide valuable insights into whether the observed alterations in memory performance, PV cell hyperexcitability and engram inhibition become more pronounced over time. Our previous work has shown that changes in pyramidal cell excitability emerge at a later stage than in PV cells, supporting the idea of progressive circuit dysfunction (Hijazi et al., 2020a). However, at these more advanced stages, additional pathological processes, such as an increased gliosis (Janota, Brites, Lemere, & Brito, 2015; Kater et al., 2023) and synaptic loss (Alonso-Nanclares, MerinoSerrais, Gonzalez, & DeFelipe, 2013; Bittner et al., 2012), will likely contribute to both electrophysiological and behavioural measurements. Furthermore, we would like to point out that the current changes observed in memory performance, PV hyperexcitability and increased inhibitory input on engram cells at 16-20 weeks of age are not modest, but already quite substantial. Our focus on these early time points in APP/PS1 mice were intentional, as it helps us understand the initial changes in Alzheimer’s disease at a circuit level and to identify therapeutic targets early intervention. What happens at later stages is certainly of interest, but beyond the scope of this study and should therefore be addressed in future studies. We have incorporated a discussion related to this point into the revised manuscript (line 602-606):

‘Moreover, it is relevant to investigate whether changes in PV and PYR cell excitability, as well as input onto engram cells in the mPFC, become more pronounced at later disease stages. Nonetheless, by focussing on early disease timepoints in the present study, we aimed to understand the initial circuit-level changes in AD and identify targets for early therapeutic intervention.’

(3) Address network hyperexcitability: Spontaneous epileptiform activity has been reported in APP/PS1 mice from 4 months of age (Reyes-Marin & Nuñez, 2017). Including EEG data or discussing this point in relation to your findings would help contextualize the observed inhibitory remodeling within broader network dysfunction. 

We thank the reviewer for this valuable input and for highlighting the study by Reyes-Marin and Nuñez (2017). In line with this, we recently reported longitudinal local field potential (LFP) recordings in freely behaving APP/PS1 Parv-Cre mice and wild type control animals between the ages of 3 to 12 months (van Heusden et al., 2023). Weekly recordings were performed in the home cage under awake mobile conditions. These data showed no indications of epileptiform activity during wakefulness, consistent with previous findings that epileptic discharges in APP/PS1 mice predominantly occur during sleep (Gureviciene et al., 2019). Recordings were obtained from the prefrontal cortex (PFC), parietal cortex and the hippocampus. In contrast, the study by Reyes-Marin and Nuñez (2017) recorded from the somatosensory cortex in anesthetized animals. Here, during spontaneous recordings, no differences were observed in delta, theta or alpha frequency bands between APP/PS1 and WT mice. Interestingly, we observed an early increase in absolute power, particularly in the hippocampus and parietal cortex from 12 to 24 weeks of age in APP/PS1 mice. In the PFC we found a shift in relative power from lower to higher frequencies and a reduction in theta power. Connectivity analyses revealed a progressive, age-dependent decline in theta/alpha coherence between the PFC and both the parietal cortex and hippocampus. Given the well-established role of PV interneurons network synchrony and coordinating theta and gamma oscillations critical for cognitive function (Sohal, Zhang, Yizhar, & Deisseroth, 2009; Xia et al., 2017), these findings support the idea of early circuit dysfunction in APP/PS1 mice. Our findings, i.e. hyperexcitability of PV cells, align with these LFP based networklevel observations. These data suggest an early shift in the E/I balance, contributing to altered oscillatory dynamics and impaired inter-regional connectivity, possibly leading to alterations in memory. However, whether the observed PV hyperexcitability in our study directly contributes to alterations in power and synchrony remains to be elucidated. Furthermore, it would be interesting to determine the individual contribution of PV cell hyperexcitability in the hippocampus versus the mPFC to network changes and concurrent memory deficits. We have added a statement on network hyperexcitability to the discussion (line 561-565). 

‘Interestingly, we recently found a progressive disruption of oscillatory network synchrony between the mPFC and hippocampus in APP/PS1 Parv-Cre mice (van Heusden et al., 2023). However, whether the observed PV cell hyperexcitability directly contributes to changes in inter-regional synchrony, and whether this leads to alterations at a network level, i.e. increased inhibitory input on engram cells, and consequently to memory deficits, remains to be elucidated in future studies.’ 

(4) Mechanisms responsible for PV hyperexcitability: Related to the previous point, a discussion of the possible underlying mechanisms, e.g., direct effects of amyloid-β, inflammatory processes, or compensatory mechanisms, would strengthen the discussion. 

We agree with the reviewer that this will strengthen the discussion. We have now added a comprehensive discussion in the revised manuscript to address potential mechanisms responsible for PV cell hyperexcitability (line 579-594).:

‘Prior studies have shown that neurons in the vicinity of amyloid beta plaques show increased excitability (Busche et al., 2008). We demonstrated that PV neurons in the CA1 are hyperexcitable and that treatment with a BACE1 inhibitors, i.e. reducing amyloid beta levels, rescues PV excitability (Hijazi et al., 2020a). In line with this, we also reported that addition of amyloid beta to hippocampal slices increases PV excitability, without altering pyramidal cell excitability (Hijazi et al., 2020a). Finally, applying amyloid beta to an induced mouse model of PV hyperexcitability further impairs PV function (Hijazi et al., 2020b). Since amyloid beta plaque load in the mPFC remains comparable between 16- and 20-week-old APP/PS1 mice, the observed increased excitability is unlikely the result of changes in insoluble amyloid beta levels. Previous data from our lab show that soluble amyloid beta is already present as early as 6 weeks of age and becomes more prominent at 24 weeks of age (Kater et al., 2023; Végh et al., 2014). The progressive increase in soluble amyloid beta levels may contribute to the emergence of PV cell hyperexcitability. We hypothesize that the hyperexcitability induced by amyloid beta may result from disrupted ion channel function, as PV neuron dysfunction can result from altered potassium (Olah et al., 2022) and sodium channel activity (Verret et al., 2012).’

(5) Excitatory-inhibitory balance: While the main focus is on increased inhibition onto engram cells, the reported increase in sEPSC frequency (Figure 5g) across genotypes suggests the presence of excitatory remodelling as well. A brief discussion of how this may interact with increased inhibition would be valuable.  

We thank the reviewer for this comment regarding the interaction between excitatory and inhibitory remodelling. We have now incorporated this discussion point into the revised manuscript (line 528-534):

‘Interestingly, both WT and APP/PS1 mice showed an increase in sEPSC frequency onto engram cells, suggesting that increased excitatory input is a consequence of memory retrieval and not affected by genotype. However, only in APP/PS1 mice, the augmented excitatory input coincided with an elevation of inhibitory input onto engram cells. The resulting imbalance between excitation and inhibition could therefore potentially disrupt the precise control of engram reactivation and contribute to the observed remote memory impairment.’

References

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Bittner, T., Burgold, S., Dorostkar, M. M., Fuhrmann, M., Wegenast-Braun, B. M., Schmidt, B., . . . Herms, J. (2012). Amyloid plaque formation precedes dendritic spine loss. Acta Neuropathologica, 124(6), 797807. doi:10.1007/s00401-012-1047-8

Busche, M. A., Eichhoff, G., Adelsberger, H., Abramowski, D., Wiederhold, K. H., Haass, C., . . . Garaschuk, O. (2008). Clusters of hyperactive neurons near amyloid plaques in a mouse model of Alzheimer's disease. Science, 321(5896), 1686-1689. doi:10.1126/science.1162844

Grienberger, C., Rochefort, N. L., Adelsberger, H., Henning, H. A., Hill, D. N., Reichwald, J., . . . Konnerth, A. (2012). Staged decline of neuronal function in vivo in an animal model of Alzheimer's disease. Nat Commun, 3, 774. doi:10.1038/ncomms1783

Gureviciene, I., Ishchenko, I., Ziyatdinova, S., Jin, N., Lipponen, A., Gurevicius, K., & Tanila, H. (2019). Characterization of Epileptic Spiking Associated With Brain Amyloidosis in APP/PS1 Mice. Front Neurol, 10, 1151. doi:10.3389/fneur.2019.01151

Hijazi, S., Heistek, T. S., Scheltens, P., Neumann, U., Shimshek, D. R., Mansvelder, H. D., . . . van Kesteren, R. E. (2020a). Early restoration of parvalbumin interneuron activity prevents memory loss and network hyperexcitability in a mouse model of Alzheimer's disease. Mol Psychiatry, 25(12), 3380-3398. doi:10.1038/s41380-019-0483-4

Hijazi, S., Heistek, T. S., van der Loo, R., Mansvelder, H. D., Smit, A. B., & van Kesteren, R. E. (2020b). Hyperexcitable Parvalbumin Interneurons Render Hippocampal Circuitry Vulnerable to Amyloid Beta. iScience, 23(7), 101271. doi:10.1016/j.isci.2020.101271

Janota, C. S., Brites, D., Lemere, C. A., & Brito, M. A. (2015). Glio-vascular changes during ageing in wild-type and Alzheimer's disease-like APP/PS1 mice. Brain Res, 1620, 153-168. doi:10.1016/j.brainres.2015.04.056

Kater, M. S. J., Huffels, C. F. M., Oshima, T., Renckens, N. S., Middeldorp, J., Boddeke, E., . . . Verheijen, M. H. G. (2023). Prevention of microgliosis halts early memory loss in a mouse model of Alzheimer's disease. Brain Behav Immun, 107, 225-241. doi:10.1016/j.bbi.2022.10.009

Kim, H. Y., Kim, H. V., Jo, S., Lee, C. J., Choi, S. Y., Kim, D. J., & Kim, Y. (2015). EPPS rescues hippocampus-dependent cognitive deficits in APP/PS1 mice by disaggregation of amyloid-β oligomers and plaques. ature Communications, 6(1), 8997. doi:10.1038/ncomms9997

Olah, V. J., Goettemoeller, A. M., Rayaprolu, S., Dammer, E. B., Seyfried, N. T., Rangaraju, S., . . . Rowan, M. J. M. (2022). Biophysical Kv3 channel alterations dampen excitability of cortical PV interneurons and contribute to network hyperexcitability in early Alzheimer’s. Elife, 11, e75316. doi:10.7554/eLife.75316

Reyes-Marin, K. E., & Nuñez, A. (2017). Seizure susceptibility in the APP/PS1 mouse model of Alzheimer's disease and relationship with amyloid β plaques. Brain Res, 1677, 93-100. doi:10.1016/j.brainres.2017.09.026

Sohal, V. S., Zhang, F., Yizhar, O., & Deisseroth, K. (2009). Parvalbumin neurons and gamma rhythms enhance cortical circuit performance. Nature, 459(7247), 698-702. doi:10.1038/nature07991

van Heusden, F. C., van Nifterick, A. M., Souza, B. C., França, A. S. C., Nauta, I. M., Stam, C. J., . . . van Kesteren, R. E. (2023). Neurophysiological alterations in mice and humans carrying mutations in APP and PSEN1 genes. Alzheimers Res Ther, 15(1), 142. doi:10.1186/s13195-023-01287-6

Végh, M. J., Heldring, C. M., Kamphuis, W., Hijazi, S., Timmerman, A. J., Li, K. W., . . . van Kesteren, R. E. (2014). Reducing hippocampal extracellular matrix reverses early memory deficits in a mouse model of Alzheimer's disease. Acta Neuropathol Commun, 2, 76. doi:10.1186/s40478-014-0076-z

Verret, L., Mann, E. O., Hang, G. B., Barth, A. M., Cobos, I., Ho, K., . . . Palop, J. J. (2012). Inhibitory interneuron deficit links altered network activity and cognitive dysfunction in Alzheimer model. Cell, 149(3), 708-721. doi:10.1016/j.cell.2012.02.046

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Zhang, W., Hao, J., Liu, R., Zhang, Z., Lei, G., Su, C., . . . Li, Z. (2011). Soluble Aβ levels correlate with cognitive deficits in the 12-month-old APPswe/PS1dE9 mouse model of Alzheimer's disease. Behavioural Brain Research, 222(2), 342-350. doi:https://doi.org/10.1016/j.bbr.2011.03.072

Author response:

Reviewer #1 (Public review):

Major Concerns:

(1) Lack of Direct Evidence for RadD-NKp46 Interaction

The central claim that RadD interacts with NKp46 is not formally demonstrated. A direct binding assay (e.g., Biacore, ELISA, or pull-down with purified proteins) is essential to support this assertion. The absence of this fundamental experiment weakens the mechanistic conclusions of the study.

The reviewer is correct. Direct assays are currently quite impossible because RadD is huge protein and it will take years to purify it. Instead, we used immunoprecipitation assays using NKp46-Ig (Author response images 1 and 2). Fusobacteria were lysed using RIPA buffer, and the lysates were centrifuged twice to separate the supernatant from the pellet (which contains the bacterial membranes). The resulting lysates were incubated overnight with 2.5 µg of purified NKp46 and protein G-beads. After thorough washing, the bound proteins were placed in sample buffer and heated at 95 °C for 8 minutes. The eluates were run on a 10% acrylamide gel and visualized by Coomassie blue staining. As can be seen the NKp46-Ig was able to precipitate protein band around 350Kd in both F. polymorphum ATCC10953 (Author response image 1) and in F. nucleatum ATCC23726 (Author response image 2).

Author response image 1. NKp46 immunoprecipitation with Fusobacterium polymorphum (ATCC 10953) lysates. The resulting lysates of supernatant and pellet of Fusobacterium were immunoprecipitated (IP) with 2.5 μg of control fusion protein (RBD-Ig) or with NKp46-Ig. A 2.5 μg of purified fusion proteins were also run on gel.

Author response image 2. NKp46 immunoprecipitation with Fusobacterium nucleatum (ATCC 23726) lysates. The resulting lysates of supernatant and pellet of Fusobacterium were immunoprecipitated (IP) with 2.5 μg of Control fusion protein (RBD-Ig) or with NKp46-Ig. 2.5 μg of purified fusion proteins were also run on gel.

(2) Figure 2: Binding Specificity and Bacterial Strains

A CEACAM1-Ig control should be included in all binding experiments to distinguish between specific and non-specific Ig interactions. There is differential Ig binding between strains ATCC 23726 and 10953. The authors should quantify RadD expression in each strain to determine if the difference in binding is due to variation in RadD levels.

No significant difference in mCEACAM-1-Ig binding was observed across multiple independent experiments. Author response image 3 shows a representative histogram showing mCEACAM-1-Ig binding to F. nucleatum ATCC 23726 and F. polymorphum ATCC 10953. Comparable binding levels were detected in both bacterial species (upper histogram). Similarly, NKp46-Ig and Ncr1-Ig fusion proteins exhibited comparable binding patterns (lower histogram). It is currently not possible to quantify RadD expression directly, as no anti-RadD antibody is available.

Author response image 3. CEACAM-1 Ig binding to Fusobacterium ATCC 23726 and ATCC 10953. Upper histograms show staining with secondary antibody alone (gray) compared to CEACAM-1 Ig (black line). Lower histograms show binding of NKp46 and Ncr1 fusion proteins to the two Fusobacterium strains. Gray represent secondary antibody controls.

(3) Figure 3: Flow Cytometry Inconsistencies and Missing Controls

What do the FITC-negative, Ig-negative events represent? The authors should clarify whether these are background signals, bacterial aggregates, or debris.

We now present the gating strategy used in these experiments (Author response image 4). Fusion negative Ig samples were the bacterial samples stained only with the secondary antibody APC (anti-human AF647). The TITC-negative represent unlabeled bacteria.

Author response image 4. Gating strategy for FITC-labeled Fusobacterium stained with fusion proteins. Bacteria were first gated as shown in the left panel. The gated population was then further analyzed in the right plot: the lower-left quadrant represents bacterial debris, the upper-left quadrant corresponds to FITC-stained bacteria only, and the upper-right quadrant shows bacteria double-positive for FITC and APC, indicating binding of the fusion proteins.

Panel B, CEACAM1-Ig binding appears markedly increased compared to WT bacteria. The reason for this enhancement should be discussed-does it reflect upregulation of the bacterial ligand or an artifact of overexpression? Fluorescence compensation should be carefully reviewed for the NKp46/NCR1-Ig binding assays to ensure that the signals are not due to spectral overlap or nonspecific binding. Importantly, binding experiments using the FadI/RadD double knockout strain are missing and should be included. This control is essential.

We don’t know why expression of CEACAM1-Ig binding is increased. Indeed, it will be nice to have the FadI/RadD double knockout strain which we currently don’t have.

In Panel E, the basis for calculating fold-change in MFI is unclear. Please indicate the reference condition to which the change is normalized.

The mean fluorescence intensity (MFI) fold change was calculated by dividing the MFI obtained from staining with the fusion proteins by the MFI of the corresponding secondary antibody control (bacteria incubated without fusion proteins).

(4) Figure 4: Binding Inhibition and Receptor Sensitivity

Panel A lacks representative FACS plots and is currently difficult to interpret.

Fusobacteria binding to CEACAM-1, NKp46, and NCR1 fusion proteins was tested in the presence of 5 and 10 mM L-arginine (Author response image 5). L-arginine inhibited the binding of NKp46-Ig and NCR1-Ig, whereas no effect was observed on CEACAM-1-Ig binding.

Author response image 5. Fusobacterium binding inhibition by L-Arginine. The figure shows the binding of CEACAM1-Ig (left panel), NKp46-Ig (middle panel), and Ncr1-Ig (right panel) in the presence of 0 mM (black), 5 mM (red), and 10 mM (blue) L-arginine.

Differences in the sensitivity of human vs. mouse NKp46 to arginine inhibition should be discussed, given species differences in receptor-ligand interactions.

Ncr1, the murine orthologue of human NKp46, shares approximately 58% sequence identity with its human counterpart (1). The observed differences in arginine-mediated inhibition of bacterial binding between mouse and human NKp46 might stem from structural differences or distinct posttranslational modifications, such as glycosylation. Indeed, prediction algorithms combined with high-performance liquid chromatography analysis revealed that Ncr1 possesses two putative novel O-glycosylation sites, of which only one is conserved in humans (2).

References

(1) Biassoni R., Pessino A., Bottino C., Pende D., Moretta L., Moretta A. The murine homologue of the human NKp46, a triggering receptor involved in the induction of natural cytotoxicity. Eur J Immunol. 1999 Mar; 29(3).

(2) Glasner A., Roth Z., Varvak A., Miletic A., Isaacson B., Bar-On Y., Jonjić S., Khalaila I., Mandelboim O. Identification of putative novel O-glycosylations in the NK killer receptor Ncr1 essential for its activity. Cell Discov. 2015 Dec 22; 1:15036.

What are the inhibition results using F. nucleatum strains deficient in FadI?

The inhibition pattern observed in the F. nucleatum ΔFadI mutant was comparable to that of the wild-type strain (Author response image 6). When cultured under identical conditions and exposed to increasing concentrations of arginine (0, 5, and 10 mM), the F. nucleatum ΔFadI strain also demonstrated a dose-dependent reduction in binding to NKp46 and Ncr1.

Author response image 6. Arginine inhibition of NKp46-Ig and Ncr1-Ig binding in F. nucleatum ΔFadI. Histograms show NKp46-Ig (A, C) and Ncr1-Ig (B, D) binding to F. nucleatum ATCC10953 ΔFadI (A and B) and to F. nucleatum ATCC23726 ΔFadI (A and B) following exposure to 5 mM and 10 mM L-Arginine. Panels (E) and (F) display the mean fluorescence intensity (MFI) quantification corresponding to (A and B) and (C and D), respectively.

In Panel B, CEACAM1-Ig and RadD-deficient bacteria must be included as negative controls for binding specificity upon anti-NKp46 blocking.

We appreciate the request to include CEACAM1-Ig and RadD-deficient bacteria as negative controls for specificity under anti-NKp46 blocking. We don’t not think it is necessary since the 02 antibody is specific for NKp46, we used other anti0NKp46 antibodies that did not block the interaction and an irrelevant antibofy, we showed that arginine produced a dose-dependent reduction in NKp46/Ncr1 binding, consistent with an arginine-inhibitable RadD interaction already shown in our manuscript (Fig. 4A). The ΔRadD strains we used already demonstrate loss of NKp46/Ncr1 binding and loss of NK-boosting activity (Figs. 3, 5). Collectively, these data establish that NKp46/Ncr1 recognition of a high-molecular-weight ligand consistent with RadD is specific and functionally relevant.

Figure 5: Functional NK Activation and Tumor Killing

In Panels B and C, the key control condition (NK cells + anti-NKp46, without bacteria) is missing. This is needed to evaluate if NKp46 recognition is involved in tumor killing. The authors should explicitly test whether pre-incubation of NK cells with bacteria enhances their anti-tumor activity.

No significant difference in NK cell cytotoxicity was observed between untreated NK cells and NK cells incubated with anti-NKp46 antibody in the absence of bacteria. Therefore, the NK + anti-NKp46 (O2) group was included as an additional control alongside the other experimental conditions shown in Figures 5b and 5c, and is presented in Author response image 7 below.

Author response image 7. NK cytotoxicity against breast cancer cell lines. NK cell cytotoxicity against T47D (left) and MCF7 (right) breast cancer cell lines. This experiment follows the format of Figure 5b and 5c, with the addition of the NK cells + O2 antibody group. No significant differences were observed when values were normalized to NK cells alone.

Could bacteria induce stress signals in tumor cells that sensitize them to NK killing? This distinction is critical.

It remains unclear whether the bacteria induce stress-related signals in tumor cells that render them more susceptible to NK cell–mediated cytotoxicity.

(6) Figure 5D: Mechanism of Peripheral Activation

It is suggested that contact between bacteria and NK cells in the periphery leads to their activation. Can the authors confirm whether this pre-activation leads to enhanced killing of tumor targets, or if bacteria-tumor co-localization is required? The literature indicates that F. nucleatum localizes intracellularly within tumor cells. If so, how is RadD accessible to NKp46 on infiltrating NK cells?

We do not expect that pre-activation of NK cells with bacteria would enhance their tumor-killing capacity. In fact, when NK cells were co-incubated with bacteria, we occasionally observed NK cell death. Although F. nucleatum can reside intracellularly, bacterial entry requires prior adhesion to tumor cells. At this stage—before internalization—the bacteria are accessible for recognition and binding by NK cells.

(8) Figure 5E and In Vivo Relevance

Surprisingly, F. nucleatum infection is associated with increased tumor burden. Does this reflect an immunosuppressive effect? Are NK cells inhibited or exhausted in infected mice (TGIT, SIGLEC7...)? If NK cell activation leads to reduced tumor control in the infected context, the role of RadD-induced activation needs further explanation. RadD-deficient bacteria, which do not activate NK cells, result in even poorer tumor control. This paradox needs to be addressed: how can NK activation impair tumor control while its absence also reduces tumor control?

Siglec-7 lacks a direct orthologue in mice, and neither mouse TIGIT nor CEACAM1 bind F. nucleatum. The increased tumor burden observed in infected mice may therefore result from bacterial interference with immune cell infiltration and accumulation within the tumor microenvironment (Parhi, L., Alon-Maimon, T., Sol, A. et al. Breast cancer colonization by Fusobacterium nucleatum accelerates tumor growth and metastatic progression. Nat Commun 11, 3259 (2020)). Consequently, the NK cells that do reach the tumor site can recognize and kill F. nucleatum–bearing tumor cells through RadD–NKp46 interactions. In the absence of RadD, this recognition is impaired, leading to reduced NK-mediated cytotoxicity and increased tumor growth.

(9) NKp46-Deficient Mice: Inconsistencies

In Ncr1⁻/⁻ mice, infection with WT or RadD-deficient F. nucleatum has no impact on tumor burden. This suggests that NKp46 is dispensable in this context and casts doubt on the physiological relevance of the proposed mechanism. This contradiction should be discussed more thoroughly.

Ncr1 is also directly involved in mediating NK cell–dependent killing of tumor cells, even in the absence of bacterial infection. Therefore, in Ncr1-deficient mice, F. nucleatum has no additional effect on tumor progression (Glasner, A., Ghadially, H., Gur, C., Stanietsky, N., Tsukerman, P., Enk, J., Mandelboim, O. Recognition and prevention of tumor metastasis by the NK receptor NKp46/NCR1. J Immunol. 2012).

Reviewer #2 (Public review):

Weaknesses:

(1) A previous study by this group (PMID: 38952680) demonstrated that RadD of F. nucleatum binds to NK cells via Siglec-7, thereby diminishing their cytotoxic potential. They further proposed that the RadD-Siglec-7 interaction could act as an immune evasion mechanism exploited by tumor cells. In contrast, the present study reports that RadD of F. nucleatum can also bind to the activating receptor NKp46 on NK cells, thereby enhancing their cytotoxic function.

Siglec-7 lacks a direct orthologue in mice, and neither mouse TIGIT nor CEACAM1 bind F. nucleatum. In contrast, NKp46 and its murine homologue, Ncr1, both recognize and bind the bacterium.

While F. nucleatum-mediated tumor progression has been documented in breast and colon cancers, the current study proposes an NK-activating role for F. nucleatum in HNSC. However, it remains unclear whether tumor-infiltrating NK cells in HNSC exhibit differential expression of NKp46 compared to Siglec-7. Furthermore, heterogeneity within the NK cell compartment, particularly in the relative abundance of NKp46⁺ versus Siglec-7⁺ subsets, may differ substantially among breast, colon, and HNSC tumors. Such differences could have been readily investigated using publicly available single-cell datasets. A deeper understanding of this subset heterogeneity in NK cells would better explain why F. nucleatum is passively associated with a favorable prognosis in HNSC but correlates with poor outcomes in breast and colon cancers.

Currently, there are no publicly available single-cell datasets suitable for characterizing NK cell heterogeneity in the context of F. nucleatum infection—particularly regarding the expression of Siglec-7, NKp46, or CEACAM1 and their potential association with poor clinical outcomes in breast, head and neck squamous cell carcinoma (HNSC), or colorectal cancer (CRC). Furthermore, no RNA-seq datasets are available for breast cancer cases specifically associated with F. nucleatum infection and poor prognosis. Therefore, we analyzed bulk RNA expression datasets for Siglec-7 and CEACAM1 and evaluated their associations with HNSC and CRC using the same patient databases utilized in our manuscript (Author response image 8). No significant differences in Siglec-7 expression were detected between HNSC and CRC samples (Author response image 8A). Although CEACAM1 mRNA levels did not differ between F. nucleatum–positive and –negative cases within either cancer type, its overall expression was higher in CRC compared to HNSC (Author response image 8B).

Author response image 8. Siglec7 and Ceacam1 expression and the prognostic effect of F. nucleatum in a tumor-type-specific manner. Comparison of Siglec7 (A) and Ceacam1 (B) expression across HNSC and CRC tumors. Log₂ expression levels of NKp46 mRNA were compared across HNSC and CRC cohorts, stratified by F. nucleatum positive and negative. Results were analyzed by one-way ANOVA with Bonferroni post hoc correction.

(2) The in vivo tumor data (Figure 5D-F) appear to contradict the authors' claims. Specifically, Figure 5E suggests that WT mice engrafted with AT3 breast tumors and inoculated with WT F. nucleatum exhibited an even greater tumor burden compared to mice not inoculated with F. nucleatum, indicating a tumor-promoting effect. This finding conflicts with the interpretation presented in both the results and discussion sections.

Siglec-7 lacks a direct orthologue in mice, and neither mouse TIGIT nor CEACAM1 bind F. nucleatum. The increased tumor burden observed in infected mice may therefore result from bacterial interference with immune cell infiltration and accumulation within the tumor microenvironment (Parhi, L., Alon-Maimon, T., Sol, A. et al. Breast cancer colonization by Fusobacterium nucleatum accelerates tumor growth and metastatic progression. Nat Commun 11, 3259 (2020)). Consequently, the NK cells that do reach the tumor site can recognize and kill F. nucleatum–bearing tumor cells through RadD–NKp46 interactions. In the absence of RadD, this recognition is impaired, leading to reduced NK-mediated cytotoxicity and increased tumor growth.

(3) Although the authors acknowledge that F. nucleatum may have tumor context-specific roles in regulating NK cell responses, it is unclear why they chose a breast cancer model in which F. nucleatum has been reported to promote tumor growth. A more appropriate choice would have been the well-established preclinical oral cancer model, such as the 4-nitroquinoline 1-oxide (4NQO)-induced oral cancer model in C57BL/6 mice, which would more directly relate to HNSC biology.

The tumor model we employed is, to date, the only model in which F. nucleatum has been shown to exert a measurable effect, which is why we selected it for our study (Parhi, L., Alon-Maimon, T., Sol, A. et al. Breast cancer colonization by Fusobacterium nucleatum accelerates tumor growth and metastatic progression. Nat Commun. 2020; 11: 3259). We have not tested the 4-nitroquinoline-1-oxide (4NQO)–induced oral cancer model, and we are uncertain whether its use would be ethically justified.

(4) Since RadD of F. nucleatum can bind to both Siglec-7 and NKp46 on NK cells, exerting opposing functional effects, the expression profiles of both receptors on intratumoral NK cells should be evaluated. This would clarify the balance between activating and inhibitory signals in the tumor microenvironment and provide a more mechanistic explanation for the observed tumor context-dependent outcomes.

This question was answered in Author response image 8 above.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review):

Summary:

The manuscript characterizes a functional peptidergic system in the echinoderm Apostichopus japonicus that is related to the widely conserved family of calcitonin/diuretic hormone 31 (CT/DH31) peptides in bilaterian animals. In vitro analysis of receptor-ligand interactions, using multiple receptor activation assays, identifies three cognate receptors for two CT-like peptides in the sea cucumber, which stimulate cAMP, calcium, and ERK signaling. Only one of these receptors clusters within the family of calcitonin and calcitonin-like receptors (CTR/CLR) in bilaterian animals, whereas two other receptors cluster with invertebrate pigment dispersing factor receptors (PDFRs). In addition, this study sheds light on the expression and in vivo functions of CT-like peptides in A. japonicus, by quantitative real-time PCR, immunohistochemistry, pharmacological experiments on body wall muscle and intestine preparations, and peptide injection and RNAi knockdown experiments. This reveals a conserved function of CT-like peptides as muscle relaxants and growth regulators in A. japonicus.

Strengths:

This work combines both in vitro and in vivo functional assays to identify a CT-like peptidergic system in an economically relevant echinoderm species, the sea cucumber A. japonicus. A major strength of the study is that it identifies three G protein-coupled receptors for AjCT-like peptides, one related to the CTR/CLR family and two related to the PDFR family. A similar finding was previously reported for the CT-related peptide DH31 in Drosophila melanogaster that activates both CT-type and PDF-type receptors. Here, the authors expand this observation to a deuterostomian animal, which suggests that receptor promiscuity is a more general feature of the CT/DH31 peptide family and that CT/DH31-like peptides may activate both CT-type and PDF-type receptors in other animals as well.

Besides the identification of receptor-ligand pairs, the downstream signaling pathways of AjCT receptors have been characterized, revealing broad and in some cases receptor-specific effects on cAMP, calcium, and ERK signaling.

Functional characterization of the CT-related peptide system in heterologous cells is complemented with ex vivo and in vivo experiments. First, peptide injection and RNAi knockdown experiments establish transcriptional regulation of all three identified receptors in response to changing AjCT peptide levels. Second, ex vivo experiments reveal a conserved role for the two CT-like peptides as muscle relaxants, which have differential effects on body wall muscle and intestine preparations. Finally, peptide injection and knockdown experiments uncover a growth-promoting role for one CT-like peptide (AjCT2). Injection of AjCT2 at high concentration, or long-term knockdown of the AjCT precursor, affects diverse growth-related parameters including weight gain rate, specific growth rate, and transcript levels of growth-regulating transcription factors. The authors also reveal a growth-promoting function for the PDFR-like receptor AjPDFR2, suggesting that this receptor mediates the effects of AjCT2 on growth.

Weaknesses:

The authors present a more detailed phylogenetic analysis in the revised version, including a larger number of species. But some clusters in the analysis are not well supported because they have only low bootstrap values. This makes it difficult to interpret the clustering in some parts of the tree.

Thank you for the reviewer’s comments. In response, we have produced a new phylogenetic analysis using the maximum likelihood method. This was done by Nayeli Escudero Castelán and Kite Jones in the Elphick group at QMUL and therefore they have been added as co-authors of this paper. The new phylogenetic tree (Figure 2, line 206) includes broad taxonomic sampling of CT-type receptors and PDF-type receptors. CRH-type receptors, which are also members of the secretin-type GPCR sub-family, have been included as an outgroup to root the tree. In the previous version the much more distantly related vasopressin/oxytocin-type receptors, which are rhodopsin-type GPCRs, were included as an outgroup. Furthermore, VIP-type receptors were also included in the previous tree but these have been omitted from the new tree because VIP receptor orthologs only occur in vertebrates and therefore they are not representative of a bilaterian GPCR family. The new tree shows high bootstrap support for key clades, notably achieving a bootstrap value of 100 for a clade comprising both deuterostomian and protostomian PDF receptors. This provides important evidence that the A. japonicus PDF-type receptors characterised in this study (AjPDFR1, AjPDFR2) are co-orthologs of the PDF-type receptor that has been characterised previously in Drosophila. Similarly, there is strong bootstrap support (100) for a clade comprising CT/DH31-type receptors and, importantly, the CT-type receptor characterised in this study (AjCTR) is positioned in a branch of this clade that comprises deuterostomian CT-type receptors (with bootstrap support of 100). Details of methods employed to produce the new receptor tree are included in lines 727-739. The new phylogenetic tree is shown below and has been incorporated into the revised manuscript (Figure 2, line 206). The description of new phylogenetic tree has also been modified accordingly in the revised manuscript (line 169-183).

References:

Bauknecht P, Jékely G. Large-Scale Combinatorial Deorphanization of Platynereis Neuropeptide GPCRs. Cell reports, 2015, 12(4), 684–693. doi:  10.1016/j.celrep.2015.06.052.

Beets I, Zels S, Vandewyer E, Demeulemeester J, et al. System-wide mapping of peptide-GPCR interactions in C. elegans. Cell reports, 2023, 42(9), 113058. doi: 10.1016/j.celrep.2023.113058.

Cardoso J C, Mc Shane J C, Li Z, et al. Revisiting the evolution of Family B1 GPCRs and ligands: Insights from mollusca. Molecular and cellular endocrinology, 2024, 586, 112192. doi: 10.1016/j.mce.2024.112192.

Gorn A H, Lin H Y, Yamin M, et al. Cloning, characterization, and expression of a human calcitonin receptor from an ovarian carcinoma cell line. The Journal of clinical investigation, 1992, 90(5), 1726–1735. doi: 10.1172/JCI116046.

Huang T, Su J, Wang X, et al. Functional Analysis and Tissue-Specific Expression of Calcitonin and CGRP with RAMP-Modulated Receptors CTR and CLR in Chickens. Animals: an open access journal from MDPI, 2024, 14(7), 1058. doi: 10.3390/ani14071058.

Johnson E C, Shafer O T, Trigg J S, et al. A novel diuretic hormone receptor in Drosophila: evidence for conservation of CGRP signaling. Journal of Experimental Biology, 2005, 208(7): 1239-1246. doi: 10.1242/jeb.01529.

McLatchie L M, Fraser N J, Main M J, et al. RAMPs regulate the transport and ligand specificity of the calcitonin-receptor-like receptor. Nature, 1998, 393(6683): 333-339. doi: 10.1038/30666.

Schwartz J, Réalis-Doyelle E, Dubos M P, et al. Characterization of an evolutionarily conserved calcitonin signaling system in a lophotrochozoan, the Pacific oyster (Crassostrea gigas). Journal of Experimental Biology, 2019, 222(13): jeb201319. doi: 10.1242/jeb.201319.

Sekiguchi T, Kuwasako K, Ogasawara M, et al. Evidence for conservation of the calcitonin superfamily and activity-regulating mechanisms in the basal chordate Branchiostoma floridae: insights into the molecular and functional evolution in chordates. Journal of Biological Chemistry, 2016, 291(5): 2345-2356. doi: 10.1074/jbc.M115.664003.

Expression of CT-like peptides was investigated both at transcript and protein level, but insight into the expression of the three peptide receptors is limited. This makes it difficult to understand the mechanism underlying the (different) functions of the two CT-like peptides in vivo. The authors identify differences in signal transduction cascades activated by each peptide, which might underpin distinct functions, but these differences were established only in heterologous cells.

We appreciate the reviewer's insightful comments. Regarding expression of CT-like peptide receptors, we have quantitatively analyzed the mRNA expression levels of the three receptors in key tissues using qRT-PCR (Figure 6, line 319) and receptor expression exhibits significant tissue-specific differences. Combined with the heterologous expression assays and In vivo functional validation, we believe our findings have provided clear mechanistic insights into the functional divergence of the two CT-like peptides. Investigation of the expression of the three receptor proteins in A. japonicus would require generation of specific antibodies, which was beyond the scope of this study. Furthermore, immunohistochemical visualization of neuropeptide receptor expression in other invertebrates has not been reported widely, which likely reflects technical difficulties in generation of antibodies that can be used to specifically detect receptor proteins that are typically expressed a low level in comparison to the neuropeptides that act as their ligands. 

We acknowledge that investigating signal transduction cascades in heterologous cells (rather than native A. japonicus cells) is a limitation. However, as a non-model organism, A. japonicus currently lacks established cell lines for such research. Therefore, using heterologous cells was the most feasible approach to examine the differential signaling cascades activated by the peptides through the three receptors. Importantly, our in vivo experiments demonstrated that long-term knockdown of either the AjCT precursor or AjPDFR2 resulted in similar and significant growth defects. The phenotypic consistency strongly suggests that AjCT2 and AjPDFR2 function within the same signaling pathway, with AjPDFR2 serving as the key receptor functionally activated by AjCT2.

The authors show overlapping phenotypes for a long-term knockdown of the AjCT precursor and the AjPDFR2 receptor, suggesting that the growth-regulating functions of AjCT2 are mediated by this receptor pathway. However, it remains unclear whether this mechanism underpins the growth-regulating function of AjCT2, until further in vivo evidence for this ligand-receptor interaction is presented. For example, the authors could investigate whether knockdown of AjPDFR2 attenuates the effects of AjCT2 peptide injection. In addition, a functional PDF system in this species remains uncharacterized, and a potential role of PDF-like peptides in growth regulation has not yet been investigated in A. japonicus. Therefore, it also remains unclear whether the ability of CT-like peptides to activate PDFRs is an evolutionary ancient property of this peptide family or whether this is an example of convergent evolution in some protostomian (Drosophila) and deuterostomian (sea cucumber) species.

Thank you for the reviewer’s insightful comments and constructive questions. We acknowledge the request for more direct evidence to demonstrate how AjCT2 functions in vivo through AjPDFR2. However, long-term knockdown of the AjCT precursor and AjPDFR2 both resulted in identical and significant growth defect phenotypes. The high phenotypic consistency, combined with the activation effect of AjCT2 on AjPDFR2 in heterologous cells, strongly suggests that they function within the same signaling pathway, with AjPDFR2 serving as the key receptor functionally activated by AjCT2. While exogenous peptide injection combined with receptor knockdown is a classic method for verifying receptor activation, phenotypic overlap itself is widely accepted in genetic research as robust evidence for pathway association (Shafer and Taghert, 2009; Van Sinay et al., 2017). A. japonicus is a non-model organism with a 3-month aestivation period in summer followed shortly by winter hibernation. During these periods, we are unable to conduct in vivo experiments. Any single experimental suggestion from reviewers could potentially require one more year of research and we have already conducted an additional year of research, in response to reviewer feedback, since submitting the original manuscript. We hope therefore that these challenges associated with working with aquatic invertebrate non-model organisms is recognized by the reviewers.

We fully agree that the functional PDF/PDFR system in A. japonicus and its potential role in growth regulation remain uncharacterized. Currently, the precursors of the PDF-type neuropeptide in echinoderms remain unidentified, which precludes clear pharmacological characterization of the two receptors. While further exploration of echinoderm PDF-type neuropeptides is still needed, our phylogenetic analysis-conducted using the maximum likelihood method with optimized parameters and rigorous sequence curation-demonstrates that the deuterostomian PDFRs (including AjPDFR1 and AjPDFR2) are positioned in a clade with the well-characterized protostomian PDFR clades with extremely high bootstrap support (value=100). Therefore, these two receptors in A. japonicus clearly belong to the PDF receptor family and our findings clearly indicate that the ability of CT-like peptides to activate PDFRs is either an evolutionarily ancient and conserved property or has arisen independently in different lineages. Details of methods employed to produce the new receptor tree are included in line 727-739. The new phylogenetic tree is shown below and has been incorporated into the revised manuscript (Figure 2, line 206). The description of new phylogenetic tree has also been modified accordingly in the revised manuscript (line 169-183).

References:

Bauknecht P, Jékely G. Large-Scale Combinatorial Deorphanization of Platynereis Neuropeptide GPCRs. Cell reports, 2015, 12(4), 684–693. doi:  10.1016/j.celrep.2015.06.052.

Beets I, Zels S, Vandewyer E, Demeulemeester J, et al. System-wide mapping of peptide-GPCR interactions in C. elegans. Cell reports, 2023, 42(9), 113058. doi: 10.1016/j.celrep.2023.113058.

Cardoso J C, Mc Shane J C, Li Z, et al. Revisiting the evolution of Family B1 GPCRs and ligands: Insights from mollusca. Molecular and cellular endocrinology, 2024, 586, 112192. doi: 10.1016/j.mce.2024.112192.

Gorn A H, Lin H Y, Yamin M, et al. Cloning, characterization, and expression of a human calcitonin receptor from an ovarian carcinoma cell line. The Journal of clinical investigation, 1992, 90(5), 1726–1735. doi: 10.1172/JCI116046.

Huang T, Su J, Wang X, et al. Functional Analysis and Tissue-Specific Expression of Calcitonin and CGRP with RAMP-Modulated Receptors CTR and CLR in Chickens. Animals: an open access journal from MDPI, 2024, 14(7), 1058. doi: 10.3390/ani14071058.

Johnson E C, Shafer O T, Trigg J S, et al. A novel diuretic hormone receptor in Drosophila: evidence for conservation of CGRP signaling. Journal of Experimental Biology, 2005, 208(7): 1239-1246. doi: 10.1242/jeb.01529.

McLatchie L M, Fraser N J, Main M J, et al. RAMPs regulate the transport and ligand specificity of the calcitonin-receptor-like receptor. Nature, 1998, 393(6683): 333-339. doi: 10.1038/30666.

Schwartz J, Réalis-Doyelle E, Dubos M P, et al. Characterization of an evolutionarily conserved calcitonin signaling system in a lophotrochozoan, the Pacific oyster (Crassostrea gigas). Journal of Experimental Biology, 2019, 222(13): jeb201319. doi: 10.1242/jeb.201319.

Sekiguchi T, Kuwasako K, Ogasawara M, et al. Evidence for conservation of the calcitonin superfamily and activity-regulating mechanisms in the basal chordate Branchiostoma floridae: insights into the molecular and functional evolution in chordates. Journal of Biological Chemistry, 2016, 291(5): 2345-2356. doi: 10.1074/jbc.M115.664003.

Shafer, O. T., & Taghert, P. H. (2009). RNA-interference knockdown of Drosophila pigment dispersing factor in neuronal subsets: the anatomical basis of a neuropeptide's circadian functions. PloS one, 4(12), e8298. doi: 10.1371/journal.pone.0008298.

Van Sinay, E., Mirabeau, O., Depuydt, G., Van Hiel, M. B., Peymen, K., Watteyne, J., Zels, S., Schoofs, L., & Beets, I. (2017). Evolutionarily conserved TRH neuropeptide pathway regulates growth in Caenorhabditis elegans. Proceedings of the National Academy of Sciences of the United States of America, 114(20), E4065–E4074. doi: 10.1073/pnas.1617392114.

Reviewer #2 (Public review):

Summary:

The authors show that A. japonicus calcitonins (AjCT1 and AjCT2) activate not only the calcitonin/calcitonin-like receptor, but they also activate the two "PDF receptors", ex vivo. They also explore secondary messenger pathways that are recruited following receptor activation. They determine the source of CT1 and CT2 using qPCR and in situ hybridization and finally test the effects of these peptides on tissue contractions, feeding and growth. This study provides solid evidence that CT1 and CT2 act as ligands for calcitonin receptors; however, evidence supporting cross-talk between CT peptides and "PDF receptors" is weak.

Strengths:

This is the first study to report pharmacological characterization of CT receptors in an echinoderm. Multiple lines of evidence in cell culture (receptor internalization and secondary messenger pathways) support this conclusion.

Weaknesses:

The authors claim that A. japonicus CTs activate "PDF" receptors and suggest that this cross-talk is evolutionary ancient since similar phenomenon also exists in the fly Drosophila melanogaster. These conclusions are not fully supported. The authors perform phylogenetic analysis to show that the two "PDF" receptors form an independent clade. The bootstrap support is quite low in a lot of instances, especially for the deuterostomian and protostomian PDFR clades which is below 30. With such low support, it is unclear if the clade comprising deuterostomian "PDFR" is in fact PDFRs and not another receptor type whose endogenous ligand (besides CT) remains to be discovered.

Thank you for the reviewer’s comments. In response, we have produced a new phylogenetic analysis using the maximum likelihood method. This was done by Nayeli Escudero Castelán and Kite Jones in the Elphick group at QMUL and therefore they have been added as co-authors of this paper. The new phylogenetic tree (Figure 2, line 206) includes broad taxonomic sampling of CT-type receptors and PDF-type receptors. CRH-type receptors, which are also members of the secretin-type GPCR sub-family, have been included as an outgroup to root the tree. In the previous version the much more distantly related vasopressin/oxytocin-type receptors, which are rhodopsin-type GPCRs, were included as an outgroup. Furthermore, VIP-type receptors were also included in the previous tree but these have been omitted from the new tree because VIP receptor orthologs only occur in vertebrates and therefore they are not representative of a bilaterian GPCR family. The new tree shows high bootstrap support for key clades, notably achieving a bootstrap value of 100 for a clade comprising both deuterostomian and protostomian PDF receptors. This provides important evidence that the A. japonicus PDF-type receptors characterized in this study (AjPDFR1, AjPDFR2) are co-orthologs of the PDF-type receptor that has been characterized previously in Drosophila. Similarly, there is strong bootstrap support (100) for a clade comprising CT/DH31-type receptors and, importantly, the CT-type receptor characterized in this study (AjCTR) is positioned in a branch of this clade that comprises deuterostomian CT-type receptors (with bootstrap support of 100). Details of methods employed to produce the new receptor tree are included in lines 727-739. The new phylogenetic tree is shown below and has been incorporated into the revised manuscript (Figure 2, line 206). The description of new phylogenetic tree has also been modified accordingly in the revised manuscript (line 169-183).

References:

Bauknecht P, Jékely G. Large-Scale Combinatorial Deorphanization of Platynereis Neuropeptide GPCRs. Cell reports, 2015, 12(4), 684–693. doi:  10.1016/j.celrep.2015.06.052.

Beets I, Zels S, Vandewyer E, Demeulemeester J, et al. System-wide mapping of peptide-GPCR interactions in C. elegans. Cell reports, 2023, 42(9), 113058. doi: 10.1016/j.celrep.2023.113058.

Cardoso J C, Mc Shane J C, Li Z, et al. Revisiting the evolution of Family B1 GPCRs and ligands: Insights from mollusca. Molecular and cellular endocrinology, 2024, 586, 112192. doi: 10.1016/j.mce.2024.112192.

Gorn A H, Lin H Y, Yamin M, et al. Cloning, characterization, and expression of a human calcitonin receptor from an ovarian carcinoma cell line. The Journal of clinical investigation, 1992, 90(5), 1726–1735. doi: 10.1172/JCI116046.

Huang T, Su J, Wang X, et al. Functional Analysis and Tissue-Specific Expression of Calcitonin and CGRP with RAMP-Modulated Receptors CTR and CLR in Chickens. Animals: an open access journal from MDPI, 2024, 14(7), 1058. doi: 10.3390/ani14071058.

Johnson E C, Shafer O T, Trigg J S, et al. A novel diuretic hormone receptor in Drosophila: evidence for conservation of CGRP signaling. Journal of Experimental Biology, 2005, 208(7): 1239-1246. doi: 10.1242/jeb.01529.

McLatchie L M, Fraser N J, Main M J, et al. RAMPs regulate the transport and ligand specificity of the calcitonin-receptor-like receptor. Nature, 1998, 393(6683): 333-339. doi: 10.1038/30666.

Schwartz J, Réalis-Doyelle E, Dubos M P, et al. Characterization of an evolutionarily conserved calcitonin signaling system in a lophotrochozoan, the Pacific oyster (Crassostrea gigas). Journal of Experimental Biology, 2019, 222(13): jeb201319. doi: 10.1242/jeb.201319.

Sekiguchi T, Kuwasako K, Ogasawara M, et al. Evidence for conservation of the calcitonin superfamily and activity-regulating mechanisms in the basal chordate Branchiostoma floridae: insights into the molecular and functional evolution in chordates. Journal of Biological Chemistry, 2016, 291(5): 2345-2356. doi: 10.1074/jbc.M115.664003.

Reviewer #2 (Recommendations for the authors):

Figure 1C: The bootstrap support is quite low in a lot of instances, especially for the deuterostomian and protostomian PDFR clades which is below 30. With such support, I would be hesitant to label the blue clade as deuterostomian PDFR for two reasons: 1) no members of this clade have been shown to be activated by a PDF-like substance and 2) the current study shows that these receptors are activated by CT-type peptides. Therefore, the phylogenetic analyses do not support the conclusions of this paper. What is the basis for calling these receptors PDFR and not CTR in light of weak phylogenetic support?

Thank you for the reviewer’s comments. In response, we have produced a new phylogenetic analysis using the maximum likelihood method. This was done by Nayeli Escudero Castelán and Kite Jones in the Elphick group at QMUL and therefore they have been added as co-authors of this paper. The new phylogenetic tree (Figure 2, line 206) includes broad taxonomic sampling of CT-type receptors and PDF-type receptors. CRH-type receptors, which are also members of the secretin-type GPCR sub-family, have been included as an outgroup to root the tree. In the previous version the much more distantly related vasopressin/oxytocin-type receptors, which are rhodopsin-type GPCRs, were included as an outgroup. Furthermore, VIP-type receptors were also included in the previous tree but these have been omitted from the new tree because VIP receptor orthologs only occur in vertebrates and therefore they are not representative of a bilaterian GPCR family. The new tree shows high bootstrap support for key clades, notably achieving a bootstrap value of 100 for a clade comprising both deuterostomian and protostomian PDF receptors. This provides important evidence that the A. japonicus PDF-type receptors characterized in this study (AjPDFR1, AjPDFR2) are co-orthologs of the PDF-type receptor that has been characterized previously in Drosophila. Similarly, there is strong bootstrap support (100) for a clade comprising CT/DH31-type receptors and, importantly, the CT-type receptor characterized in this study (AjCTR) is positioned in a branch of this clade that comprises deuterostomian CT-type receptors (with bootstrap support of 100). Details of methods employed to produce the new receptor tree are included in lines 727-739 The new phylogenetic tree is shown below and has been incorporated into the revised manuscript (Figure 2, line 206). The description of new phylogenetic tree has also been modified accordingly in the revised manuscript (line 169-183).

We agree with the reviewer that no members of the PDF-type receptor clade in deuterostomes have yet been shown to be activated by a PDF-like substance. That is because the precursors of the PDF-type neuropeptides in echinoderms remain unidentified so far, which precludes clear pharmacological characterization of these receptors within the deuterostomian PDFR clade. However, the new phylogenetic tree now provides strong support (bootstrap value = 100) for the clade comprising deuterostomian and protostomian PDFRs, confirming the classification of AjPDFR1 and AjPDFR2 as PDF-type receptors. 

References:

Bauknecht P, Jékely G. Large-Scale Combinatorial Deorphanization of Platynereis Neuropeptide GPCRs. Cell reports, 2015, 12(4), 684–693. doi:  10.1016/j.celrep.2015.06.052.

Beets I, Zels S, Vandewyer E, Demeulemeester J, et al. System-wide mapping of peptide-GPCR interactions in C. elegans. Cell reports, 2023, 42(9), 113058. doi: 10.1016/j.celrep.2023.113058.

Cardoso J C, Mc Shane J C, Li Z, et al. Revisiting the evolution of Family B1 GPCRs and ligands: Insights from mollusca. Molecular and cellular endocrinology, 2024, 586, 112192. doi: 10.1016/j.mce.2024.112192.

Gorn A H, Lin H Y, Yamin M, et al. Cloning, characterization, and expression of a human calcitonin receptor from an ovarian carcinoma cell line. The Journal of clinical investigation, 1992, 90(5), 1726–1735. doi: 10.1172/JCI116046.

Huang T, Su J, Wang X, et al. Functional Analysis and Tissue-Specific Expression of Calcitonin and CGRP with RAMP-Modulated Receptors CTR and CLR in Chickens. Animals: an open access journal from MDPI, 2024, 14(7), 1058. doi: 10.3390/ani14071058.

Johnson E C, Shafer O T, Trigg J S, et al. A novel diuretic hormone receptor in Drosophila: evidence for conservation of CGRP signaling. Journal of Experimental Biology, 2005, 208(7): 1239-1246. doi: 10.1242/jeb.01529.

McLatchie L M, Fraser N J, Main M J, et al. RAMPs regulate the transport and ligand specificity of the calcitonin-receptor-like receptor. Nature, 1998, 393(6683): 333-339. doi: 10.1038/30666.

Schwartz J, Réalis-Doyelle E, Dubos M P, et al. Characterization of an evolutionarily conserved calcitonin signaling system in a lophotrochozoan, the Pacific oyster (Crassostrea gigas). Journal of Experimental Biology, 2019, 222(13): jeb201319. doi: 10.1242/jeb.201319.

Sekiguchi T, Kuwasako K, Ogasawara M, et al. Evidence for conservation of the calcitonin superfamily and activity-regulating mechanisms in the basal chordate Branchiostoma floridae: insights into the molecular and functional evolution in chordates. Journal of Biological Chemistry, 2016, 291(5): 2345-2356. doi: 10.1074/jbc.M115.664003.

The new results following AjCT and AjPDFR2 knockdown are a welcome addition. While this additional evidence supports the claim that AjCT could mediate its effects via AjPDFR2, this evidence does not show that AjCT acts as an endogenous ligand for PDFR in vivo. In combination with the weak phylogenetic analyses, I would recommend the authors to key down their claims that they have functionally characterized a PDFR (in the title and text).

Thank you for your insightful comments and we do understand the reviewer’s concern. 

Regarding “the weak phylogenetic analyses”, as highlighted above, we have produced a new phylogenetic tree (Fig 2, line 206) that provides strong bootstrap support for the clade comprising deuterostome and protostome PDF-type receptors. For this reason, it is our opinion that inclusion of “pigment-dispersing factor-type receptors” in the title of the paper is appropriate. The details of phylogenetic analysis method were added in line 727-739, and the updated phylogenetic tree has been incorporated into the revised manuscript (Figure 2, line 206). The description of new phylogenetic tree has also been modified accordingly in the revised manuscript (line 169-183). Besides, long-term knockdown of the AjCT precursor and AjPDFR2 both resulted in identical and significant growth defect phenotypes. And the observation of phenotypic overlap is widely accepted in genetic research as strong evidence for pathway association (Shafer and Taghert, 2009; Van Sinay et al., 2017). This high degree of phenotypic consistency, coupled with our in vitro finding that AjCT2 specifically activates AjPDFR2, strongly supports the conclusion that AjCT2 and AjPDFR2 function within the same signaling pathway in vivo, with AjPDFR2 serving as the key receptor functionally activated by AjCT2.

References:

Shafer, O. T., & Taghert, P. H. (2009). RNA-interference knockdown of Drosophila pigment dispersing factor in neuronal subsets: the anatomical basis of a neuropeptide's circadian functions. PloS one, 4(12), e8298. doi: 10.1371/journal.pone.0008298.

Van Sinay, E., Mirabeau, O., Depuydt, G., Van Hiel, M. B., Peymen, K., Watteyne, J., Zels, S., Schoofs, L., & Beets, I. (2017). Evolutionarily conserved TRH neuropeptide pathway regulates growth in Caenorhabditis elegans. Proceedings of the National Academy of Sciences of the United States of America, 114(20), E4065–E4074. doi: 10.1073/pnas.1617392114.

Since there is no formal logic defining the use of "type" vs "like" vs "related", I would encourage the authors to use one term (of their choice) to avoid unnecessary confusion. Or another possibility is that these relationships are defined at some point in the manuscript so that it becomes clear to the reader.

Thank you for the reviewer’s comments. The “CT-related peptides” has defined in the Introduction (line 54-58). As per your suggestion, we have now defined both “CT-type peptides” and “CT-like peptides” in the Introduction (line 76-79). “CT-type peptides” are characterized by an N-terminal disulphide bridge, whereas “CT-like peptides” (diuretic hormone 31 (DH31)-type peptides) lack this feature. Additionally, in accordance with the definitions, we have corrected these three descriptions in the revised manuscript (line 80, 83, 88 for “CT-type peptides”) to ensure consistent and accurate usage of these terms.

"To provide in vivo evidence supporting CT-mediated activation of "PDF" receptors, we conducted the following experiments: Firstly, we confirmed that AjPDFR1 and AjPDFR2were the functional receptors of AjCT1and AjCT2 (Figure 2, 3 and 4). Secondly, injection of AjCT2 and siAjCTP1/2-1 in vivo induced corresponding changes in AjPDFR1and AjPDFR2expression levels in the intestine (Figure 8C, 9A, 9B and 9C)."

None of these experiments provide direct evidence that CT activates PDFR in vivo. The functional studies are indeed a welcome addition but they cannot discriminate between correlation and causation.

Thank you for the reviewer’s insightful comments. We agree that the functional studies do not constitute direct proof that CT’s activation of PDFR in vivo. However, we observed identical and significant growth defect phenotypes following long-term knockdown of the AjCT precursor and the AjPDFR2. This high degree of phenotypic congruence, combined with the established in vitro activation of AjPDFR2 by AjCT2, provides strong support for the conclusion that AjCT2 acts as the key endogenous ligand activating the AjPDFR2 signaling pathway in vivo. Importantly, such phenotypic overlap has been widely accepted in genetic research as strong evidence for functional pathway association (Shafer and Taghert, 2009; Van Sinay et al., 2017).

References:

Shafer, O. T., & Taghert, P. H. (2009). RNA-interference knockdown of Drosophila pigment dispersing factor in neuronal subsets: the anatomical basis of a neuropeptide's circadian functions. PloS one, 4(12), e8298. doi: 10.1371/journal.pone.0008298.

Van Sinay, E., Mirabeau, O., Depuydt, G., Van Hiel, M. B., Peymen, K., Watteyne, J., Zels, S., Schoofs, L., & Beets, I. (2017). Evolutionarily conserved TRH neuropeptide pathway regulates growth in Caenorhabditis elegans. Proceedings of the National Academy of Sciences of the United States of America, 114(20), E4065–E4074. doi: 10.1073/pnas.1617392114.

working towards a sweet-spot

achive what's above the threshold that is required

working towards a sweet-spot

achive what's above the threshold that is required

https://hyp.is/95kSDrJPEfCvcauZZHECLg/www.futuresplatform.com/blog/s-curve-analysis-foresight

working towards a sweet-spot

REALize what's just above the threshold that is required

groan zone of perseverance where progress appears to be stalled for a long long time

working towards a sweet-spot

achive what's above the threshold that is required

from

Author response:

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

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

We thank reviewer #1 for their positive evaluation of our paper. Obviously, we agree with the reviewer that the paper would be much stronger if BOTH effects – spike increase and decrease – would be found in BOTH patients in their corresponding fMRI regions (lateral and medial fusiform gyrus) (also in the same hemisphere). Nevertheless, we clearly acknowledge this limitation in the (revised) version of the manuscript (p.8: Material and Methods section).

Note that with respect to the fMRI data, our results are not surprising, as we indicate in the manuscript: BOLD increases to faces (relative to nonface objects) are typically found in the LatFG and BOLD decreases in the medialFG (in the revised version, we have added the reference to an early neuroimaging paper that describes this dissociation clearly:

Pelphrey, K. A., Mack, P. B., Song, A., Güzeldere, G., & McCarthy, G. Faces evoke spatially differentiated patterns of BOLD activation and deactivation. Neuroreport 14, 955–959 (2003).

This pattern of increase/decrease in fMRI can be appreciated in both patients on Figure 2, although one has to consider both the transverse and coronal slices to appreciate it.

Regarding electrophysiological data, in the current paper, one could think that P1 shows only increases to faces, and P2 would show only decreases (irrespective of the region). However, that is not the case since 11% of P1’s face-selective units are decreases (89% are increases) and 4% of P2’s face-selective units are increases. This has now been made clearer in the revised manuscript (p.5).

As the reviewer is certainly aware, the number and positions of the electrodes are based on strict clinical criteria, and we will probably never encounter a situation with two neighboring (macro-micro hybrid electrodes), one with microelectrodes ending up in the lateral MidFG, the other in the medial MidFG, in the same patient. If there is no clinical value for the patient, this cannot be done.

The only thing we can do is to strengthen these results in the future by collecting data on additional patients with an electrode either in the lateral or the medial FG, together with fMRI. But these are the only two patients we have been able to record so far with electrodes falling unambiguously in such contrasted regions and with large (and comparable) measures.

While we acknowledge that the results may be unique because of the use of 2 contrasted patients only (and this is why the paper is a short report), the data is compelling in these 2 cases, and we are confident that it will be replicated in larger cohorts in the future.

Finally, information regarding ethics approval has been provided in the paper.

Reviewer #2 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

The authors claim that the results tell us about both 1) face-selectivity in the fusiform gyrus, and 2) the physiological basis of the BOLD signal. However, I would like to see more of the data that supports the first claim, and I am not sure the second claim is supported.

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

We thank reviewer #2 for their positive evaluation of our paper. We understand the reviewer’s point, and we partly agree. Where we respectfully disagree is that the finding of absolute suppression is critical for the claim of the paper: finding an identical contrast between the two regions in terms of RELATIVE increase/decrease of face-selective activity in fMRI and spiking activity is already novel and informative. Where we agree with the reviewer is that the absolute suppression could be more documented: it wasn’t, due to space constraints (brief report). We provide below an example of a neuron showing absolute suppression to faces (P2), as also requested in the recommendations to authors. In the frequency domain, there is only a face-selective response (1.2 Hz and harmonics) but no significant response at 6 Hz (common general visual response). In the time-domain, relative to face onset, the response drops below baseline level. It means that this neuron has baseline (non-periodic) spontaneous spiking activity that is actively suppressed when a face appears.

Author response image 1.

(2) I am not sure how much light the results shed on the physiological basis of the BOLD signal. The authors write that the results reveal "that BOLD decreases can be due to relative, but also absolute, spike suppression in the human brain" (line 120). But I think to make this claim, you would need a region that exclusively had neurons showing absolute suppression, not a region with a mix of neurons, some showing absolute suppression and some showing relative suppression, as here. The responses of both groups of neurons contribute to the measured BOLD signal, so it seems impossible to tell from these data how absolute suppression per se drives the BOLD response.

It is a fact that we find both kinds of responses in the same region. We cannot tell with this technique if neurons showing relative vs. absolute suppression of responses are spatially segregated for instance (e.g., forming two separate sub-regions) or are intermingled. And we cannot tell from our data how absolute suppression per se drives the BOLD response. In our view, this does not diminish the interest and originality of the study, but the statement "that BOLD decreases can be due to relative, but also absolute, spike suppression in the human brain” has been rephrased in the revised manuscript: "that BOLD decreases can be due to relative, or absolute (or a combination of both), spike suppression in the human brain”.

Reviewer #3 (Public review):

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

Strengths:

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

Weaknesses:

My major concerns are two-fold:

(i) There is a paucity of data; Thus, more information (results and methods) is warranted; and in particular there is no comparison between the fMRI data and the SEEG data.

We thank reviewer #3 for their positive evaluation of our paper. If the reviewer means paucity of data presentation, we agree and we provide more presentation below, although the methods and results information appear as complete to us. The comparison between fMRI and SEEG is there, but can only be indirect (i.e., collected at different times and not related on a trial-by-trial basis for instance). In addition, our manuscript aims at providing a short empirical contribution to further our understanding of the relationship between neural responses and BOLD signal, not to provide a model of neurovascular coupling.

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

We understand the concern of the reviewer, but we respectfully disagree that our paradigm cannot distinguish between lower firing rate to faces vs. suppression of response to faces. Indeed, since the stimuli are presented periodically (6 Hz), we can objectively distinguish stimulus-related activity from spontaneous neuronal firing. The baseline corresponds to spikes that are non-periodic, i.e., unrelated to the (common face and object) stimulation. For a subset of neurons, even this non-periodic baseline activity is suppressed, above and beyond the suppression of the 6 Hz response illustrated on Figure 2. We mention it in the manuscript, but we agree that we do not present illustrations of such decrease in the time-domain for SU, which we did not consider as being necessary initially (please see below for such presentation).

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

We answer to more specific requests for additional evidence below, but the reviewer should be aware that this is a short report, which reaches the word limit. In our view, the group average neural data should be sufficient to support the conclusions, and the example neurons are there for illustration. And while we cannot provide the raster plots for a large number of neurons, the anonymized data is made available at:

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

As mentioned above the comparison between fMRI and SEEG is indirect (i.e., collected at different times and not related on a trial-by-trial basis for instance) and would not allow to make such a model.

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

The data has been analyzed comprehensively, but we would not be able to show all neurons with such significant visual responses and face-selective responses.

(c) The neuron shown in E shows cyclical responses tied to the onset of the stimuli, is this the visual response?

Correct, it’s the visual response at 6 Hz.

If so, why is there an increase in the firing rate of the neuron before the face stimulus is shown in time 0?

Because the stimulation is continuous. What is displayed at 0 is the onset of the face stimulus, with each face stimulus being preceded by 4 images of nonface objects.

The neuron's data seems different than the average response across neurons; This raises a concern about interpreting the average response across neurons in panel F which seems different than the single neuron responses

The reviewer is correct, and we apologize for the confusion. This is because the average data on panel F has been notch-filtered for the 6 Hz (and harmonic responses), as indicated in the methods (p.11): ‘a FFT notch filter (filter width = 0.05 Hz) was then applied on the 70 s single or multi-units time-series to remove the general visual response at 6 Hz and two additional harmonics (i.e., 12 and 18 Hz)’.

Here is the same data without the notch-filter (the 6Hz periodic response is clearly visible):

Author response image 2.

For sake of clarity, we prefer presenting the notch-filtered data in the paper, but the revised version makes it clear in the figure caption that the average data has been notch-filtered.

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

We agree with the reviewer that this is interesting, but again we do not think that it is necessary for the point made in the present paper. Responses in these regions appear rather heterogenous, and we are currently working on a longer paper with additional SEEG data (other patients tested for shorter sessions) to define and quantify the face-selective neurons in the MidFusiform gyrus with this approach (without relating it to the fMRI contrast as reported here).

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

We agree with the reviewer and have modified Figure 2 accordingly in the revised manuscript.

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

The fast periodic paradigm to measure neural face-selectivity has been used in tens of studies since its original reports:

• in EEG: Rossion et al., 2015: https://doi.org/10.1167/15.1.18

• in SEEG: Jonas et al., 2016: https://doi.org/10.1073/pnas.1522033113

In this paradigm, the face-selective response spreads to several harmonics (1.2 Hz, 2.4 Hz, 3.6 Hz, etc.) (which are summed for quantifying the total face-selective amplitude). This is illustrated below by the averaged single units’ SNR spectra across all recording sessions for both participants.

Author response image 3.

There is no unique phase-value, each harmonic being associated with a phase-value, so that the timing cannot be unambiguously extracted from phase values. Instead, the onset latency is computed directly from the time-domain responses, which is more straightforward and reliable than using the phase. Note that the present paper is not about the specific time-courses of the different types of neurons, which would require a more comprehensive report, but which is not necessary to support the point made in the present paper about the SEEG-fMRI sign relationship.

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

Face-selectivity is defined as a DIFFERENTIAL response to faces compared to objects, not necessarily a larger response to faces. So yes, face-selectivity in P1 is an increase in response to faces and P2 a reduction in response to faces.

Additional methods

(a) it is unclear if the SSVEP analyses of neural responses were done on the spikes or the raw electrical signal. If the former, how is the SSVEP frequency analysis done on discrete data like action potentials?

The FFT is applied directly on spike trains using Matlab’s discrete Fourier Transform function. This function is suitable to be applied to spike trains in the same way as to any sampled digital signal (here, the microwires signal was sampled at 30 kHz, see Methods).

In complementary analyses, we also attempted to apply the FFT on spike trains that had been temporally smoothed by convolving them with a 20ms square window (Le Cam et al., 2023, cited in the paper ). This did not change the outcome of the frequency analyses in the frequency range we are interested in. We have also added one sentence with information in the methods section about spike detection (p.10).

(b) it is unclear why the onset time was shifted by 33ms; one can measure the phase of the response relative to the cycle onset and use that to estimate the delay between the onset of a stimulus and the onset of the response. Adding phase information will be useful.

The onset time was shifted by 33ms because the stimuli are presented with a sinewave contrast modulation (i.e., at 0ms, the stimulus has 0% contrast). 100% contrast is reached at half a stimulation cycle, which is 83.33ms here, but a response is likely triggered before reaching 100% contrast. To estimate the delay between the start of the sinewave (0% contrast) and the triggering of a neural response, we tested 7 SEEG participants with the same images presented in FPVS sequences either as a sinewave contrast (black line) modulation or as a squarewave (i.e. abrupt) contrast modulation (red line). The 33ms value is based on these LFP data obtained in response to such sinewave stimulation and squarewave stimulation of the same paradigm. This delay corresponds to 4 screen refresh frames (120 Hz refresh rate = 8.33ms by frame) and 35% of the full contrast, as illustrated below (please see also Retter, T. L., & Rossion, B. (2016). Uncovering the neural magnitude and spatio-temporal dynamics of natural image categorization in a fast visual stream. Neuropsychologia, 91, 9–28).

Author response image 4.

(2) Interpretation of suppression:

The SSVEP paradigm alternates between 2 conditions: faces and objects and has no baseline; In other words, responses to faces are measured relative to the baseline response to objects so that any region that contains neurons that have a lower firing rate to faces than objects is bound to show a lower response in the SSVEP signal. Therefore, because the experiment does not have a true baseline (e.g. blank screen, with no visual stimulation) this experimental design cannot distinguish between lower firing rate to faces vs suppression of response to faces.

The strongest evidence put forward for suppression is the response of non-visual neurons that was also reduced when patients looked at faces, but since these are non-visual neurons, it is unclear how to interpret the responses to faces.

We understand this point, but how does the reviewer know that these are non-visual neurons? Because these neurons are located in the visual cortex, they are likely to be visual neurons that are not responsive to non-face objects. In any case, as the reviewer writes, we think it’s strong evidence for suppression.

We thank all three reviewers for their positive evaluation of our paper and their constructive comments.

Author response:

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

To the Senior Editor and the Reviewing Editor:

We sincerely appreciate the valuable comments provided by the reviewers, the reviewing editor, and the senior editor. Based on our last response and revision, we are confused by the two limitations noted in the eLife assessment. 

(1) benchmarking against comparable methods is limited.

In our last revision, we added the comparison experiments with TNDM, as the reviewers requested. Additionally, it is crucial to emphasize that our evaluation of decoding capabilities of behaviorally relevant signals has been benchmarked against the performance of the ANN on raw signals, which, as Reviewer #1 previously noted, nearly represents the upper limit of performance. Consequently, we believe that our benchmarking methods are sufficiently strong.

(2) some observations may be a byproduct of their method, and may not constitute new scientific observations.

We believe that our experimental results are sufficient to demonstrate that our conclusions are not byproducts of d-VAE based on three reasons:

(1) The d-VAE, as a latent variable model, adheres to the population doctrine, which posits that latent variables are responsible for generating the activities of individual neurons. The goal of such models is to maximize the explanation of the raw signals. At the signal level, the only criterion we can rely on is neural reconstruction performance, in which we have achieved unparalleled results. Thus, it is inappropriate to focus on the mixing process during the model's inference stage while overlooking the crucial de-mixing process during the generation stage and dismissing the significance of our neural reconstruction results. For more details, please refer to the first point in our response to Q4 from Reviewer #4.

(2) The criterion that irrelevant signals should contain minimal information can effectively demonstrate that our conclusions are not by-products of d-VAE. Unfortunately, the reviewers seem to have overlooked this criterion. For more details, please refer to the third point in our response to Q4 from Reviewer #4

(3) Our synthetic experimental results also substantiate that our conclusions are not byproducts of d-VAE. However, it appears the reviewers did not give these results adequate consideration. For more details, please refer to the fourth point in our response to Q4 from Reviewer #4.

Furthermore, our work presents not just "a useful method" but a comprehensive framework. Our study proposes, for the first time, a framework for defining, extracting, and validating behaviorally relevant signals. In our current revision, to clearly distinguish between d-VAE and other methods, we have formalized the extraction of behaviorally relevant signals into a mathematical optimization problem. To our knowledge, current methods have not explicitly proposed extracting behaviorally relevant signals, nor have they identified and addressed the key challenges of extracting relevant signals. Similarly, existing research has not yet defined and validated behaviorally relevant signals. For more details, please refer to our response to Q1 from Reviewer #4.

Based on these considerations, we respectfully request that you reconsider the eLife assessment of our work. We greatly appreciate your time and attention to this matter.

The main revisions made to the manuscript are as follows:

(1) We have formalized the extraction of behaviorally relevant signals into a mathematical optimization problem, enabling a clearer distinction between d-VAE and other models.

(2) We have moderated the assertion about linear readout to highlight its conjectural nature and have broadened the discussion regarding this conclusion. 

(3) We have elaborated on the model details of d-VAE and have removed the identifiability claim.

To Reviewer #1

Q1: “As reviewer 3 also points out, I would, however, caution to interpret this as evidence for linear read-out of the motor system - your model performs a non-linear transformation, and while this is indeed linearly decodable, the motor system would need to do something similar first to achieve the same. In fact to me it seems to show the opposite, that behaviour-related information may not be generally accessible to linear decoders (including to down-stream brain areas).”

Thank you for your comments. It's important to note that the conclusions we draw are speculative and not definitive. We use terms like "suggest" to reflect this uncertainty. To further emphasize the conjectural nature of our conclusions, we have deliberately moderated our tone.

The question of whether behaviorally-relevant signals can be accessed by linear decoders or downstream brain regions hinges on the debate over whether the brain employs a strategy of filtering before decoding. If the brain employs such a strategy, the brain can probably access these signals. In our opinion, it is likely that the brain utilizes this strategy.

Given the existence of behaviorally relevant signals, it is reasonable to assume that the brain has intrinsic mechanisms to differentiate between relevant and irrelevant signals. There is growing evidence suggesting that the brain utilizes various mechanisms, such as attention and specialized filtering, to suppress irrelevant signals and enhance relevant signals [1-3]. Therefore, it is plausible that the brain filters before decoding, thereby effectively accessing behaviorally relevant signals.

Thank you for your valuable feedback.

(1) Sreenivasan, Sameet, and Ila Fiete. "Grid cells generate an analog error-correcting code for singularly precise neural computation." Nature neuroscience 14.10 (2011): 1330-1337.

(2) Schneider, David M., Janani Sundararajan, and Richard Mooney. "A cortical filter that learns to suppress the acoustic consequences of movement." Nature 561.7723 (2018): 391-395.

(3) Nakajima, Miho, L. Ian Schmitt, and Michael M. Halassa. "Prefrontal cortex regulates sensory filtering through a basal ganglia-to-thalamus pathway." Neuron 103.3 (2019): 445-458.

Q2: “As in my initial review, I would also caution against making strong claims about identifiability although this work and TNDM seem to show that in practise such methods work quite well. CEBRA, in contrast, offers some theoretical guarantees, but it is not a generative model, so would not allow the type of analysis done in this paper. In your model there is a para,eter \alpha to balance between neural and behaviour reconstruction. This seems very similar to TNDM and has to be optimised - if this is correct, then there is manual intervention required to identify a good model.”

Thank you for your comments. 

Considering your concerns about our identifiability claims and the fact that identifiability is not directly relevant to the core of our paper, we have removed content related to identifiability.

Firstly, our model is based on the pi-VAE, which also has theoretical guarantees. However, it is important to note that all such theoretical guarantees (including pi-VAE and CEBRA) are based on certain assumptions that cannot be validated as the true distribution of latent variables remains unknown.

Secondly, it is important to clarify that the identifiability of latent variables does not impact the conclusions of this paper, nor does this paper make specific conclusions about the model's latent variables. Identifiability means that distinct latent variables correspond to distinct observations. If multiple latent variables can generate the same observation, it becomes impossible to determine which one is correct given the observation, which leads to the issue of nonidentifiability. Notably, our analysis focuses on the generated signals, not the latent variables themselves, and thus the identifiability of these variables does not affect our findings. 

Our approach, dedicated to extracting these signals, distinctly differs from methods such as TNDM, which focuses on extracting behaviorally relevant latent dynamics. To clearly set apart d-VAE from other models, we have framed the extraction of behaviorally relevant signals as the following mathematical optimization problem:

where 𝑥# denotes generated behaviorally-relevant signals, 𝑥 denotes raw noisy signals, 𝐸(⋅,⋅) demotes reconstruction loss, and 𝑅(⋅) denotes regularization loss. It is important to note that while both d-VAE and TNDM employ reconstruction loss, relying solely on this term is insufficient for determining the optimal degree of similarity between the generated and raw noisy signals. The key to accurately extracting behaviorally relevant signals lies in leveraging prior knowledge about these signals to determine the optimal similarity degree, encapsulated by 𝑅(𝒙𝒓).  Other studies have not explicitly proposed extracting behaviorally-relevant signals, nor have they identified and addressed the key challenges involved in extracting relevant signals. Consequently, our approach is distinct from other methods.

Thank you for your valuable feedback.

Q3: “Somewhat related, I also found that the now comprehensive comparison with related models shows that the using decoding performance (R2) as a metric for model comparison may be problematic: the R2 values reported in Figure 2 (e.g. the MC_RTT dataset) should be compared to the values reported in the neural latent benchmark, which represent well-tuned models (e.g. AutoLFADS). The numbers (difficult to see, a table with numbers in the appendix would be useful, see: https://eval.ai/web/challenges/challenge-page/1256/leaderboard) seem lower than what can be obtained with models without latent space disentanglement. While this does not necessarily invalidate the conclusions drawn here, it shows that decoding performance can depend on a variety of model choices, and may not be ideal to discriminate between models. I'm also surprised by the low neural R2 for LFADS I assume this is condition-averaged) - LFADS tends to perform very well on this metric.”

Thank you for your comments. The dataset we utilized is not from the same day as the neural latent benchmark dataset. Notably, there is considerable variation in the length of trials within the RTT paradigm, and the dataset lacks explicit trial information, rendering trial-averaging unsuitable. Furthermore, behaviorally relevant signals are not static averages devoid of variability; even behavioral data exhibits variability. We computed the neural R2 using individual trials rather than condition-averaged responses. 

Thank you for your valuable feedback.

Q4: “One statement I still cannot follow is how the prior of the variational distribution is modelled. You say you depart from the usual Gaussian prior, but equation 7 seems to suggest there is a normal prior. Are the parameters of this distribution learned? As I pointed out earlier, I however suspect this may not matter much as you give the prior a very low weight. I also still am not sure how you generate a sample from the variational distribution, do you just draw one for each pass?”

Thank you for your questions.

The conditional distribution of prior latent variables 𝑝%(𝒛|𝒚) is a Gaussian distribution, but the distribution of prior latent variables 𝑝(𝒛) is a mixture Gaussian distribution. The distribution of prior latent variables 𝑝(𝒛) is:

where denotes the empirical distribution of behavioral variables

𝒚, and 𝑁 denotes the number of samples, 𝒚(𝒊) denotes the 𝒊th sample, δ(⋅) denotes the Dirac delta function, and 𝑝%(𝒛|𝒚) denotes the conditional distribution of prior latent variables given the behavioral variables parameterized by network 𝑚. Based on the above equation, we can see that 𝑝(𝒛) is not a Gaussian distribution, it is a Gaussian mixture model with 𝑁 components, which is theoretically a universal approximator of continuous probability densities.

Learning this prior is important, as illustrated by our latent variable visualizations, which are not a Gaussian distribution. Upon conducting hypothesis testing for both latent variables and behavioral variables, neither conforms to Gaussian distribution (Lilliefors test and Kolmogorov-Smirnov test). Consequently, imposing a constraint on the latent variables towards N(0,1) is expected to affect performance adversely.

Regarding sampling, during training process, we draw only one sample from the approximate posterior distribution . It is worth noting that drawing multiple samples or one sample for each pass does not affect the experimental results. After training, we can generate a sample from the prior by providing input behavioral data 𝒚(𝒊) and then generating corresponding samples via and . To extract behaviorally-relevant signals from raw signals, we use and .

Thank you for your valuable feedback.

Q5: “(1) I found the figures good and useful, but the text is, in places, not easy to follow. I think the manuscript could be shortened somewhat, and in some places more concise focussed explanations would improve readability.

(2) I would not call the encoding "complex non-linear" - non-linear is a clear term, but complex can mean many things (e.g. is a quadratic function complex?) ”

Thank you for your recommendation. We have revised the manuscript for enhanced clarity.  We call the encoding “complex nonlinear” because neurons encode information with varying degrees of nonlinearity, as illustrated in Fig. 3b, f, and Fig. S3b.

Thank you for your valuable feedback.

To Reviewer #2

Q1: “I still remain unconvinced that the core findings of the paper are "unexpected". In the response to my previous Specific Comment #1, they say "We use the term 'unexpected' due to the disparity between our findings and the prior understanding concerning neural encoding and decoding." However, they provide no citations or grounding for why they make those claims. What prior understanding makes it unexpected that encoding is more complex than decoding given the entropy, sparseness, and high dimensionality of neural signals (the "encoding") compared to the smoothness and low dimensionality of typical behavioural signals (the "decoding")?” 

Thank you for your comments. We believe that both the complexity of neural encoding and the simplicity of neural decoding in motor cortex are unexpected.

The Complexity of Neural Encoding: As noted in the Introduction, neurons with small R2 values were traditionally considered noise and consequently disregarded, as detailed in references [1-3]. However, after filtering out irrelevant signals, we discovered that these neurons actually contain substantial amounts of behavioral information, previously unrecognized. Similarly, in population-level analyses, neural signals composed of small principal components (PCs) are often dismissed as noise, with analyses typically utilizing only between 6 and 18 PCs [4-10]. Yet, the discarded PC signals nonlinearly encode significant amounts of information, with practically useful dimensions found to range between 30 and 40—far exceeding the usual number analyzed. These findings underscore the complexity of neural encoding and are unexpected.

The Simplicity of Neural Decoding: In the motor cortex, nonlinear decoding of raw signals has been shown to significantly outperform linear decoding, as evidenced in references [11,12]. Interestingly, after separating behaviorally relevant and irrelevant signals, we observed that the linear decoding performance of behaviorally relevant signals is nearly equivalent to that of nonlinear decoding—a phenomenon previously undocumented in the motor cortex. This discovery is also unexpected.

Thank you for your valuable feedback.

(1) Georgopoulos, Apostolos P., Andrew B. Schwartz, and Ronald E. Kettner. "Neuronal population coding of movement direction." Science 233.4771 (1986): 1416-1419.

(2) Hochberg, Leigh R., et al. "Reach and grasp by people with tetraplegia using a neurally controlled robotic arm." Nature 485.7398 (2012): 372-375. 

(3) Inoue, Yoh, et al. "Decoding arm speed during reaching." Nature communications 9.1 (2018): 5243.

(4) Churchland, Mark M., et al. "Neural population dynamics during reaching." Nature 487.7405 (2012): 51-56.

(5) Kaufman, Matthew T., et al. "Cortical activity in the null space: permitting preparation without movement." Nature neuroscience 17.3 (2014): 440-448.

(6) Elsayed, Gamaleldin F., et al. "Reorganization between preparatory and movement population responses in motor cortex." Nature communications 7.1 (2016): 13239.

(7) Sadtler, Patrick T., et al. "Neural constraints on learning." Nature 512.7515 (2014): 423426.

(8) Golub, Matthew D., et al. "Learning by neural reassociation." Nature neuroscience 21.4 (2018): 607-616.

(9) Gallego, Juan A., et al. "Cortical population activity within a preserved neural manifold underlies multiple motor behaviors." Nature communications 9.1 (2018): 4233.

(10) Gallego, Juan A., et al. "Long-term stability of cortical population dynamics underlying consistent behavior." Nature neuroscience 23.2 (2020): 260-270.

(11) Glaser, Joshua I., et al. "Machine learning for neural decoding." Eneuro 7.4 (2020).

(12) Willsey, Matthew S., et al. "Real-time brain-machine interface in non-human primates achieves high-velocity prosthetic finger movements using a shallow feedforward neural network decoder." Nature Communications 13.1 (2022): 6899.

Q2: “I still take issue with the premise that signals in the brain are "irrelevant" simply because they do not correlate with a fixed temporal lag with a particular behavioural feature handchosen by the experimenter. In the response to my previous review, the authors say "we employ terms like 'behaviorally-relevant' and 'behaviorally-irrelevant' only regarding behavioral variables of interest measured within a given task, such as arm kinematics during a motor control task.". This is just a restatement of their definition, not a response to my concern, and does not address my concern that the method requires a fixed temporal lag and continual decoding/encoding. My example of reward signals remains. There is a huge body of literature dating back to the 70s on the linear relationships between neural and activity and arm kinematics; in a sense, the authors have chosen the "variable of interest" that proves their point. This all ties back to the previous comment: this is mostly expected, not unexpected, when relating apparently-stochastic, discrete action potential events to smoothly varying limb kinematics.”

Thank you for your comments. 

Regarding the experimenter's specification of behavioral variables of interest, we followed common practice in existing studies [1, 2]. Regarding the use of fixed temporal lags, we followed the same practice as papers related to the dataset we use, which assume fixed temporal lags [3-5]. Furthermore, many studies in the motor cortex similarly use fixed temporal lags [68].

Concerning the issue of rewards, in the paper you mentioned [9], the impact of rewards occurs after the reaching phase. It's important to note that in our experiments, we analyze only the reaching phase, without any post-movement phase. 

If the impact of rewards can be stably reflected in the signals in the reaching phase of the subsequent trial, and if the reward-induced signals do not interfere with decoding—since these signals are harmless for decoding and beneficial for reconstruction—our model is likely to capture these signals. If the signals induced by rewards during the reaching phase are randomly unstable, our model will likely be unable to capture them.

If the goal is to extract post-movement neural activity from both rewarded and unrewarded trials, and if the neural patterns differ between these conditions, one could replace the d-VAE's regression loss, used for continuous kinematics decoding, with a classification loss tailored to distinguish between rewarded and unrewarded conditions.

To clarify the definition, we have revised it in the manuscript. Specifically, before a specific definition, we briefly introduce the relevant signals and irrelevant signals. Behaviorally irrelevant signals refer to those not directly associated with the behavioral variables of interest and may include noise or signals from variables of no interest. In contrast, behaviorally relevant signals refer to those directly related to the behavioral variables of interest. For instance, rewards in the post-movement phase are not directly related to behavioral variables (kinematics) in the reaching movement phase.

It is important to note that our definition of behaviorally relevant signals not only includes decoding capabilities but also specific requirement at the signal level, based on two key requirements:

(1) they should closely resemble raw signals to preserve the underlying neuronal properties without becoming so similar that they include irrelevant signals. (encoding requirement), and  (2) they should contain behavioral information as much as possible (decoding requirement). Signals that meet both requirements are considered effective behaviorally relevant signals. In our study, we assume raw signals are additively composed of behaviorally-relevant and irrelevant signals. We define irrelevant signals as those remaining after subtracting relevant signals from raw signals. Therefore, we believe our definition is clearly articulated. 

Thank you for your valuable feedback.

(1) Sani, Omid G., et al. "Modeling behaviorally relevant neural dynamics enabled by preferential subspace identification." Nature Neuroscience 24.1 (2021): 140-149.

(2) Buetfering, Christina, et al. "Behaviorally relevant decision coding in primary somatosensory cortex neurons." Nature neuroscience 25.9 (2022): 1225-1236.

(3) Wang, Fang, et al. "Quantized attention-gated kernel reinforcement learning for brain– machine interface decoding." IEEE transactions on neural networks and learning systems 28.4 (2015): 873-886.

(4) Dyer, Eva L., et al. "A cryptography-based approach for movement decoding." Nature biomedical engineering 1.12 (2017): 967-976.

(5) Ahmadi, Nur, Timothy G. Constandinou, and Christos-Savvas Bouganis. "Robust and accurate decoding of hand kinematics from entire spiking activity using deep learning." Journal of Neural Engineering 18.2 (2021): 026011.

(6) Churchland, Mark M., et al. "Neural population dynamics during reaching." Nature 487.7405 (2012): 51-56.

(7) Kaufman, Matthew T., et al. "Cortical activity in the null space: permitting preparation without movement." Nature neuroscience 17.3 (2014): 440-448.

(8) Elsayed, Gamaleldin F., et al. "Reorganization between preparatory and movement population responses in motor cortex." Nature communications 7.1 (2016): 13239.

(9) Ramkumar, Pavan, et al. "Premotor and motor cortices encode reward." PloS one 11.8 (2016): e0160851.

Q3: “The authors seem to have missed the spirit of my critique: to say "linear readout is performed in motor cortex" is an over-interpretation of what their model can show.”

Thank you for your comments. It's important to note that the conclusions we draw are speculative and not definitive. We use terms like "suggest" to reflect this uncertainty. To further emphasize the conjectural nature of our conclusions, we have deliberately moderated our tone.

The question of whether behaviorally-relevant signals can be accessed by downstream brain regions hinges on the debate over whether the brain employs a strategy of filtering before decoding. If the brain employs such a strategy, the brain can probably access these signals. In our view, it is likely that the brain utilizes this strategy.

Given the existence of behaviorally relevant signals, it is reasonable to assume that the brain has intrinsic mechanisms to differentiate between relevant and irrelevant signals. There is growing evidence suggesting that the brain utilizes various mechanisms, such as attention and specialized filtering, to suppress irrelevant signals and enhance relevant signals [1-3]. Therefore, it is plausible that the brain filters before decoding, thereby effectively accessing behaviorally relevant signals.

Regarding the question of whether the brain employs linear readout, given the limitations of current observational methods and our incomplete understanding of brain mechanisms, it is challenging to ascertain whether the brain employs a linear readout. In many cortical areas, linear decoders have proven to be sufficiently accurate. Consequently, numerous studies [4, 5, 6], including the one you referenced [4], directly employ linear decoders to extract information and formulate conclusions based on the decoding results. Contrary to these approaches, our research has compared the performance of linear and nonlinear decoders on behaviorally relevant signals and found their decoding performance is comparable. Considering both the decoding accuracy and model complexity, our results suggest that the motor cortex may utilize linear readout to decode information from relevant signals. Given the current technological limitations, we consider it reasonable to analyze collected data to speculate on the potential workings of the brain, an approach that many studies have also embraced [7-10]. For instance, a study [7] deduces strategies the brain might employ to overcome noise by analyzing the structure of recorded data and decoding outcomes for new stimuli.

Thank you for your valuable feedback.

(1) Sreenivasan, Sameet, and Ila Fiete. "Grid cells generate an analog error-correcting code for singularly precise neural computation." Nature neuroscience 14.10 (2011): 1330-1337.

(2) Schneider, David M., Janani Sundararajan, and Richard Mooney. "A cortical filter that learns to suppress the acoustic consequences of movement." Nature 561.7723 (2018): 391-395.

(3) Nakajima, Miho, L. Ian Schmitt, and Michael M. Halassa. "Prefrontal cortex regulates sensory filtering through a basal ganglia-to-thalamus pathway." Neuron 103.3 (2019): 445-458.

(4) Jurewicz, Katarzyna, et al. "Irrational choices via a curvilinear representational geometry for value." bioRxiv (2022): 2022-03.

(5) Hong, Ha, et al. "Explicit information for category-orthogonal object properties increases along the ventral stream." Nature neuroscience 19.4 (2016): 613-622.

(6) Chang, Le, and Doris Y. Tsao. "The code for facial identity in the primate brain." Cell 169.6 (2017): 1013-1028.

(7) Ganmor, Elad, Ronen Segev, and Elad Schneidman. "A thesaurus for a neural population code." Elife 4 (2015): e06134.

(8) Churchland, Mark M., et al. "Neural population dynamics during reaching." Nature 487.7405 (2012): 51-56.

(9) Gallego, Juan A., et al. "Cortical population activity within a preserved neural manifold underlies multiple motor behaviors." Nature communications 9.1 (2018): 4233.

(10) Gallego, Juan A., et al. "Long-term stability of cortical population dynamics underlying consistent behavior." Nature neuroscience 23.2 (2020): 260-270.

Q4: “Agreeing with my critique is not sufficient; please provide the data or simulations that provides the context for the reference in the fano factor. I believe my critique is still valid.”

Thank you for your comments. As we previously replied, Churchland's research examines the variability of neural signals across different stages, including the preparation and execution phases, as well as before and after the target appears. Our study, however, focuses exclusively on the movement execution phase. Consequently, we are unable to produce comparative displays similar to those in his research. Intuitively, one might expect that the variability of behaviorally relevant signals would be lower; however, since no prior studies have accurately extracted such signals, the specific FF values of behaviorally relevant signals remain unknown. Therefore, presenting these values is meaningful, and can provide a reference for future research. While we cannot compare FF across different stages, we can numerically compare the values to the Poisson count process. An FF of 1 indicates a Poisson firing process, and our experimental data reveals that most neurons have an FF less than 1, indicating that the variance in firing counts is below the mean.  Thank you for your valuable feedback.

To Reviewer #4

Q1: “Overall, studying neural computations that are behaviorally relevant or not is an important problem, which several previous studies have explored (for example PSID in (Sani et al. 2021), TNDM in (Hurwitz et al. 2021), TAME-GP in (Balzani et al. 2023), pi-VAE in (Zhou and Wei 2020), and dPCA in (Kobak et al. 2016), etc). However, this manuscript does not properly put their work in the context of such prior works. For example, the abstract states "One solution is to accurately separate behaviorally-relevant and irrelevant signals, but this approach remains elusive", which is not the case given that these prior works have done that. The same is true for various claims in the main text, for example "Furthermore, we found that the dimensionality of primary subspace of raw signals (26, 64, and 45 for datasets A, B, and C) is significantly higher than that of behaviorally-relevant signals (7, 13, and 9), indicating that using raw signals to estimate the neural dimensionality of behaviors leads to an overestimation" (line 321). This finding was presented in (Sani et al. 2021) and (Hurwitz et al. 2021), which is not clarified here. This issue of putting the work in context has been brought up by other reviewers previously but seems to remain largely unaddressed. The introduction is inaccurate also in that it mixes up methods that were designed for separation of behaviorally relevant information with those that are unsupervised and do not aim to do so (e.g., LFADS). The introduction should be significantly revised to explicitly discuss prior models/works that specifically formulated this behavior separation and what these prior studies found, and how this study differs.”  

Thank you for your comments. Our statement about “One solution is to accurately separate behaviorally-relevant and irrelevant signals, but this approach remains elusive” is accurate. To our best knowledge, there is no prior works to do this work--- separating accurate behaviorally relevant neural signals at both single-neuron and single-trial resolution. The works you mentioned have not explicitly proposed extracting behaviorally relevant signals, nor have they identified and addressed the key challenges of extracting relevant signals, namely determining the optimal degree of similarity between the generated relevant signals and raw signals. Those works focus on the latent neural dynamics, rather than signal level.

To clearly set apart d-VAE from other models, we have framed the extraction of behaviorally relevant signals as the following mathematical optimization problem:

where 𝒙𝒓 denotes generated behaviorally-relevant signals, 𝒙 denotes raw noisy signals, 𝐸(⋅,⋅) demotes reconstruction loss, and 𝑅(⋅) denotes regularization loss. It is important to note that while both d-VAE and TNDM employ reconstruction loss, relying solely on this term is insufficient for determining the optimal degree of similarity between the generated and raw noisy signals. The key to accurately extracting behaviorally relevant signals lies in leveraging prior knowledge about these signals to determine the optimal similarity degree, encapsulated by 𝑅(𝒙𝒓). All the works you mentioned did not have the key part 𝑅(𝒙𝒓).

Regarding the dimensionality estimation, the dimensionality of neural manifolds quantifies the degrees of freedom required to describe population activity without significant information loss.

There are two differences between our work and PSID and TNDM. 

First, the dimensions they refer to are fundamentally different from ours. The dimensionality we describe pertains to a linear subspace, where a neural dimension or neural mode or principal component basis, , with N representing the number of neurons. However, the vector length of a neural mode of PSID and our approach differs; PSID requires concatenating multiple time steps T, essentially making , TNDM, on the other hand, involves nonlinear dimensionality reduction, which is different from linear dimensionality reduction.

Second, we estimate neural dimensionality by explaining the variance of neural signals, whereas PSID and TNDM determine dimensionality through decoding performance saturation. It is important to note that the dimensionality at which decoding performance saturates may not accurately reflect the true dimensionality of neural manifolds, as some dimensions may contain redundant information that does not enhance decoding performance.

We acknowledge that while LFADS can generate signals that contain some behavioral information, it was not specifically designed to do so. Following your suggestion, we have removed this reference from the Introduction.

Thank you for your valuable feedback.

Q2: “Claims about linearity of "motor cortex" readout are not supported by results yet stated even in the abstract. Instead, what the results support is that for decoding behavior from the output of the dVAE model -- that is trained specifically to have a linear behavior readout from its embedding -- a nonlinear readout does not help. This result can be biased by the very construction of the dVAE's loss that encourages a linear readout/decoding from embeddings, and thus does not imply a finding about motor cortex.”

Thank you for your comments. We respectfully disagree with the notion that the ability of relevant signals to be linearly decoded is due to constraints that allow embedding to be linearly decoded. Embedding involves reorganizing or transforming the structure of original signals, and they can be linearly decoded does not mean the corresponding signals can be decoded linearly.

Let's clarify this with three intuitive examples:

Example 1: Image denoising is a well-established field. Whether employing supervised or blind denoising methods [1, 2], both can effectively recover the original image. This denoising process closely resembles the extraction of behaviorally relevant signals from raw signals. Consider if noisy images are not amenable to linear decoding (classification); would removing the noise enable linear decoding? The answer is no. Typically, the noise in images captured under normal conditions is minimal, yet even the clear images remain challenging to decode linearly.

Example 2: Consider the task of face recognition, where face images are set against various backgrounds, in this context, the pixels representing the face corresponds to relevant signals, while the background pixels are considered irrelevant. Suppose a network is capable of extracting the face pixels and the resulting embedding can be linearly decoded. Can the face pixels themselves be linearly decoded? The answer is no. If linear decoding of face pixels were feasible, the challenging task of face recognition could be easily resolved by merely extracting the face from the background and training a linear classifier.

Example 3: In the MNIST dataset, the background is uniformly black, and its impact is minimal. However, linear SVM classifiers used directly on the original pixels significantly underperform compared to non-linear SVMs.

In summary, embedding involves reorganizing the structure of the original signals through a feature transformation function. However, the reconstruction process can recover the structure of the original signals from the embedding. The fact that the structure of the embedding can be linearly decoded does not imply that the structure of the original signals can be linearly decoded in the same way. It is inappropriate to focus on the compression process without equally considering the reconstruction process.

Thank you for your valuable feedback.

(1) Mao, Xiao-Jiao, Chunhua Shen, and Yu-Bin Yang. "Image restoration using convolutional auto-encoders with symmetric skip connections." arXiv preprint arXiv:1606.08921 (2016).

(2) Lehtinen, Jaakko, et al. "Noise2Noise: Learning image restoration without clean data." International Conference on Machine Learning. International Machine Learning Society, 2018.

Q3: “Related to the above, it is unclear what the manuscript means by readout from motor cortex. A clearer definition of "readout" (a mapping from what to what?) in general is needed. The mapping that the linearity/nonlinearity claims refer to is from the *inferred* behaviorally relevant neural signals, which themselves are inferred nonlinearly using the VAE. This should be explicitly clarified in all claims, i.e., that only the mapping from distilled signals to behavior is linear, not the whole mapping from neural data to behavior. Again, to say the readout from motor cortex is linear is not supported, including in the abstract.” 

Thank you for your comments. We have revised the manuscript to make it more clearly. Thank you for your valuable feedback.

Q4: “Claims about individual neurons are also confounded. The d-VAE distilling processing is a population level embedding so the individual distilled neurons are not obtainable on their own without using the population data. This population level approach also raises the possibility that information can leak from one neuron to another during distillation, which is indeed what the authors hope would recover true information about individual neurons that wasn't there in the recording (the pixel denoising example). The authors acknowledge the possibility that information could leak to a neuron that didn't truly have that information and try to rule it out to some extent with some simulations and by comparing the distilled behaviorally relevant signals to the original neural signals. But ultimately, the distilled signals are different enough from the original signals to substantially improve decoding of low information neurons, and one cannot be sure if all of the information in distilled signals from any individual neuron truly belongs to that neuron. It is still quite likely that some of the improved behavior prediction of the distilled version of low-information neurons is due to leakage of behaviorally relevant information from other neurons, not the former's inherent behavioral information. This should be explicitly acknowledged in the manuscript.”

Thank you for your comments. We value your insights regarding the mixing process. However, we are confident in the robustness of our conclusions. We respectfully disagree with the notion that the small R2 values containing significant information are primarily due to leakage, and we base our disagreement on four key reasons.

(1) Neural reconstruction performance is a reliable and valid criterion.

The purpose of latent variable models is to explain neuronal activity as much as possible. Given the fact that the ground truth of behaviorally-relevant signals, the latent variables, and the generative model is unknow, it becomes evident that the only reliable reference at the signal level is the raw signals. A crucial criterion for evaluating the reliability of latent variable models (including latent variables and generated relevant signals) is their capability to effectively explain the raw signals [1]. Consequently, we firmly maintain the belief that if the generated signals closely resemble the raw signals to the greatest extent possible, in accordance with an equivalence principle, we can claim that these obtained signals faithfully retain the inherent properties of single neurons. 

Reviewer #4 appears to focus on the compression (mixing) process without giving equal consideration to the reconstruction (de-mixing) process. Numerous studies have demonstrated that deep autoencoders can reconstruct the original signal very effectively. For example, in the field of image denoising, autoencoders are capable of accurately restoring the original image [2, 3]. If one persistently focuses on the fact of mixing and ignores the reconstruction （demix） process, even if the only criterion that we can rely on at the signal level is high, one still won't acknowledge it. If this were the case, many problems would become unsolvable. For instance, a fundamental criterion for latent variable models is their ability to explain the original data. If the ground truth of the latent variables remains unknown and the reconstruction criterion is disregarded, how can we validate the effectiveness of the model, the validity of the latent variables, or ensure that findings related to latent variables are not merely by-products of the model? Therefore, we disagree with the aforementioned notion. We believe that as long as the reconstruction performance is satisfactory, the extracted signals have successfully retained the characteristics of individual neurons.

In our paper, we have shown in various ways that our generated signals sufficiently resemble the raw signals, including visualizing neuronal activity (Fig. 2m, Fig. 3i, and Fig. S5), achieving the highest performance among competitors (Fig. 2d, h, l), and conducting control analyses. Therefore, we believe our results are reliable. 

(1) Cunningham, J.P. and Yu, B.M., 2014. Dimensionality reduction for large-scale neural recordings. Nature neuroscience, 17(11), pp.1500-1509.

(2) Mao, Xiao-Jiao, Chunhua Shen, and Yu-Bin Yang. "Image restoration using convolutional auto-encoders with symmetric skip connections." arXiv preprint arXiv:1606.08921 (2016).

(3) Lehtinen, Jaakko, et al. "Noise2Noise: Learning image restoration without clean data." International Conference on Machine Learning. International Machine Learning Society, 2018.

(2) There is no reason for d-VAE to add signals that do not exist in the original signals.

(1) Adding signals that does not exist in the small R2 neurons would decrease the reconstruction performance. This is because if the added signals contain significant information, they will not resemble the irrelevant signals which contain no information, and thus, the generated signals will not resemble the raw signals. The model optimizes towards reducing the reconstruction loss, and this scenario deviates from the model's optimization direction. It is worth mentioning that when the model only has reconstruction loss without the interference of decoding loss, we believe that information leakage does not happen. Because the model can only be optimized in a direction that is similar to the raw signals; adding non-existent signals to the generated signals would increase the reconstruction loss, which is contrary to the objective of optimization. 

(2) Information carried by these additional signals is redundant for larger R2 neurons, thus they do not introduce new information that can enhance the decoding performance of the neural population, which does not benefit the decoding loss.

Based on these two points, we believe the model would not perform such counterproductive and harmful operations.

(3) The criterion that irrelevant signals should contain minimal information can effectively rule out the leakage scenario.

The criterion that irrelevant signals should contain minimal information is very important, but it seems that reviewer #4 has continuously overlooked their significance. If the model's reconstruction is insufficient, or if additional information is added (which we do not believe will happen), the residuals would decode a large amount of information, and this criterion would exclude selecting such signals. To clarify, if we assume that x, y, and z denote the raw, relevant, and irrelevant signals of smaller R2 neurons, with x=y+z, and the extracted relevant signals become y+m, the irrelevant signals become z-m in this case. Consequently, the irrelevant signals contain a significant amount of information.

We presented the decoding R2 for irrelevant signals in real datasets under three distillation scenarios: a bias towards reconstruction (alpha=0, an extreme case where the model only has reconstruction loss without decoding loss), a balanced trade-off, and a bias towards decoding (alpha=0.9), as detailed in Table 1. If significant information from small R2 neurons leaks from large R2 neurons, the irrelevant signals should contain a large amount of information. However, our results indicate that the irrelevant signals contain only minimal information, and their performance closely resembles that of the model training solely with reconstruction loss, showing no significant differences (P > 0.05, Wilcoxon rank-sum test). When the model leans towards decoding, some useful information will be left in the residuals, and irrelevant signals will contain a substantial amount of information, as observed in Table 1, alpha=0.9. Therefore, we will not choose these signals for analysis.

In conclusion, the criterion that irrelevant signals should contain minimal information is a very effective measure to exclude undesirable signals.

Author response table 1.

Decoding R2 of irrelevant signals

(4) Synthetic experiments can effectively rule out the leakage scenario.

In the absence of ground truth data, synthetic experiments serve as an effective method for validating models and are commonly employed [1-3]. 

Our experimental results demonstrate that d-VAE can effectively extract neural signals that more closely resemble actual behaviorally relevant signals (Fig. S2g).  If there were information leakage, it would decrease the similarity to the ground truth signals, hence we have ruled out this possibility. Moreover, in synthetic experiments with small R2 neurons (Fig. S10), results also demonstrate that our model could make these neurons more closely resemble ground truth relevant signals and recover their information. 

In summary, synthetic experiments strongly demonstrate that our model can recover obscured neuronal information, rather than adding signals that do not exist.

(1) Pnevmatikakis, Eftychios A., et al. "Simultaneous denoising, deconvolution, and demixing of calcium imaging data." Neuron 89.2 (2016): 285-299.

(2) Schneider, Steffen, Jin Hwa Lee, and Mackenzie Weygandt Mathis. "Learnable latent embeddings for joint behavioural and neural analysis." Nature 617.7960 (2023): 360-368.

(3) Zhou, Ding, and Xue-Xin Wei. "Learning identifiable and interpretable latent models of high-dimensional neural activity using pi-VAE." Advances in Neural Information Processing Systems 33 (2020): 7234-7247.

Based on these four points, we are confident in the reliability of our results. If Reviewer #4 considers these points insufficient, we would highly appreciate it if specific concerns regarding any of these aspects could be detailed.

Thank you for your valuable feedback.

Q5: “Given the nuances involved in appropriate comparisons across methods and since two of the datasets are public, the authors should provide their complete code (not just the dVAE method code), including the code for data loading, data preprocessing, model fitting and model evaluation for all methods and public datasets. This will alleviate concerns and allow readers to confirm conclusions (e.g., figure 2) for themselves down the line.”

Thanks for your suggestion.

Our codes are now available on GitHub at https://github.com/eric0li/d-VAE. Thank you for your valuable feedback.

Q6: “Related to 1) above, the authors should explore the results if the affine network h(.) (from embedding to behavior) was replaced with a nonlinear ANN. Perhaps linear decoders would no longer be as close to nonlinear decoders. Regardless, the claim of linearity should be revised as described in 1) and 2) above, and all caveats should be discussed.”

Thank you for your suggestion. We appreciate your feasible proposal that can be empirically tested. Following your suggestion, we have replaced the decoding of the latent variable z to behavior y with a nonlinear neural network, specifically a neural network with a single hidden layer. The modified model is termed d-VAE2. We applied the d-VAE2 to the real data, and selected the optimal alpha through the validation set. As shown in Table 1, results demonstrate that the performance of KF and ANN remains comparable. Therefore, the capacity to linearly decode behaviorally relevant signals does not stem from the linear decoding of embeddings.

Author response table 2.

Decoding R2 of behaviorally relevant signals obtained by d-VAE2

Additionally, it is worth noting that this approach is uncommon and is considered somewhat inappropriate according to the Information Bottleneck theory [1]. According to the Information Bottleneck theory, information is progressively compressed in multilayer neural networks, discarding what is irrelevant to the output and retaining what is relevant. This means that as the number of layers increases, the mutual information between each layer's embedding and the model input gradually decreases, while the mutual information between each layer's embedding and the model output gradually increases. For the decoding part, if the embeddings that is not closest to the output (behaviors) is used, then these embeddings might contain behaviorally irrelevant signals. Using these embeddings to generate behaviorally relevant signals could lead to the inclusion of irrelevant signals in the behaviorally relevant signals.

To demonstrate the above statement, we conducted experiments on the synthetic data. As shown in Table 2, we present the performance (neural R2 between the generated signals and the ground truth signals) of both models at several alpha values around the optimal alpha of dVAE (alpha=0.9) selected by the validation set. The experimental results show that at the same alpha value, the performance of d-VAE2 is consistently inferior to that of d-VAE, and d-VAE2 requires a higher alpha value to achieve performance comparable to d-VAE, and the best performance of d-VAE2 is inferior to that of d-VAE.

Author response table 3.

Neural R2 between generated signals and real behaviorally relevant signals

Thank you for your valuable feedback.

(1) Shwartz-Ziv, Ravid, and Naftali Tishby. "Opening the black box of deep neural networks via information." arXiv preprint arXiv:1703.00810 (2017).

Q7: “The beginning of the section on the "smaller R2 neurons" should clearly define what R2 is being discussed. Based on the response to previous reviewers, this R2 "signifies the proportion of neuronal activity variance explained by the linear encoding model, calculated using raw signals". This should be mentioned and made clear in the main text whenever this R2 is referred to.”

Thank you for your suggestion. We have made the modifications in the main text. Thank you for your valuable feedback.

Q8: “Various terms require clear definitions. The authors sometimes use vague terminology (e.g., "useless") without a clear definition. Similarly, discussions regarding dimensionality could benefit from more precise definitions. How is neural dimensionality defined? For example, how is "neural dimensionality of specific behaviors" (line 590) defined? Related to this, I agree with Reviewer 2 that a clear definition of irrelevant should be mentioned that clarifies that relevance is roughly taken as "correlated or predictive with a fixed time lag". The analyses do not explore relevance with arbitrary time lags between neural and behavior data.”

Thanks for your suggestion. We have removed the “useless” statements and have revised the statement of “the neural dimensionality of specific behaviors” in our revised manuscripts.

Regarding the use of fixed temporal lags, we followed the same practice as papers related to the dataset we use, which assume fixed temporal lags [1-3]. Furthermore, many studies in the motor cortex similarly use fixed temporal lags [4-6]. To clarify the definition, we have revised the definition in our manuscript. For details, please refer to the response to Q2 of reviewer #2 and our revised manuscript. We believe our definition is clearly articulated.

Thank you for your valuable feedback.

(1) Wang, Fang, et al. "Quantized attention-gated kernel reinforcement learning for brain– machine interface decoding." IEEE transactions on neural networks and learning systems 28.4 (2015): 873-886.

(2) Dyer, Eva L., et al. "A cryptography-based approach for movement decoding." Nature biomedical engineering 1.12 (2017): 967-976.

(3) Ahmadi, Nur, Timothy G. Constandinou, and Christos-Savvas Bouganis. "Robust and accurate decoding of hand kinematics from entire spiking activity using deep learning." Journal of Neural Engineering 18.2 (2021): 026011.

(4) Churchland, Mark M., et al. "Neural population dynamics during reaching." Nature 487.7405 (2012): 51-56.

(5) Kaufman, Matthew T., et al. "Cortical activity in the null space: permitting preparation without movement." Nature neuroscience 17.3 (2014): 440-448.

(6) Elsayed, Gamaleldin F., et al. "Reorganization between preparatory and movement population responses in motor cortex." Nature communications 7.1 (2016): 13239. 

Q9: “CEBRA itself doesn't provide a neural reconstruction from its embeddings, but one could obtain one via a regression from extracted CEBRA embeddings to neural data. In addition to decoding results of CEBRA (figure S3), the neural reconstruction of CEBRA should be computed and CEBRA should be added to Figure 2 to see how the behaviorally relevant and irrelevant signals from CEBRA compare to other methods.”

Thank you for your question. Modifying CEBRA is beyond the scope of our work. As CEBRA is not a generative model, it cannot obtain behaviorally relevant and irrelevant signals, and therefore it lacks the results presented in Fig. 2. To avoid the same confusion encountered by reviewers #3 and #4 among our readers, we have opted to exclude the comparison with CEBRA. It is crucial to note, as previously stated, that our assessment of decoding capabilities has been benchmarked against the performance of the ANN on raw signals, which almost represents the upper limit of performance. Consequently, omitting CEBRA does not affect our conclusions.

Thank you for your valuable feedback.

Q10: “Line 923: "The optimal hyperparameter is selected based on the lowest averaged loss of five-fold training data." => why is this explained specifically under CEBRA? Isn't the same criteria used for hyperparameters of other methods? If so, clarify.”

Thank you for your question. The hyperparameter selection for CEBRA follows the practice of the original CEBRA paper. The hyperparameter selection for generative models is detailed in the Section “The strategy for selecting effective behaviorally-relevant signals”.  Thank you for your valuable feedback.

Author response:

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

Reviewer #1 (Public Review):

In this paper, the authors evaluate the utility of brain age derived metrics for predicting cognitive decline by performing a 'commonality' analysis in a downstream regression that enables the different contribution of different predictors to be assessed. The main conclusion is that brain age derived metrics do not explain much additional variation in cognition over and above what is already explained by age. The authors propose to use a regression model trained to predict cognition ('brain cognition') as an alternative suited to applications of cognitive decline. While this is less accurate overall than brain age, it explains more unique variance in the downstream regression.  

Importantly, in this revision, we clarified that we did not intend to use Brain Cognition as an alternative approach. This is because, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. Here we made this point more explicit and further stated that the relationship between Brain Cognition and fluid cognition indicates the upper limit of Brain Age’s capability in capturing fluid cognition. By examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age. 

REVISED VERSION: while the authors have partially addressed my concerns, I do not feel they have addressed them all. I do not feel they have addressed the weight instability and concerns about the stacked regression models satisfactorily.

Please see our responses to Reviewer #1 Public Review #3 below

I also must say that I agree with Reviewer 3 about the limitations of the brain age and brain cognition methods conceptually. In particular that the regression model used to predict fluid cognition will by construction explain more variance in cognition than a brain age model that is trained to predict age. This suffers from the same problem the authors raise with brain age and would indeed disappear if the authors had a separate measure of cognition against which to validate and were then to regress this out as they do for age correction. I am aware that these conceptual problems are more widespread than this paper alone (in fact throughout the brain age literature), so I do not believe the authors should be penalised for that. However, I do think they can make these concerns more explicit and further tone down the comments they make about the utility of brain cognition. I have indicated the main considerations about these points in the recommendations section below. 

Thank you so much for raising this point. We now have the following statement in the introduction and discussion to address this concern (see below). 

Briefly, we made it explicit that, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. That is, the relationship between Brain Cognition and fluid cognition indicates the upper limit of Brain Age’s capability in capturing fluid cognition. More importantly, by examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age. And this is the third goal of this present study. 

From Introduction:

“Third and finally, certain variation in fluid cognition is related to brain MRI, but to what extent does Brain Age not capture this variation? To estimate the variation in fluid cognition that is related to the brain MRI, we could build prediction models that directly predict fluid cognition (i.e., as opposed to chronological age) from brain MRI data. Previous studies found reasonable predictive performances of these cognition-prediction models, built from certain MRI modalities (Dubois et al., 2018; Pat, Wang, Anney, et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022). Analogous to Brain Age, we called the predicted values from these cognition-prediction models, Brain Cognition. The strength of an out-of-sample relationship between Brain Cognition and fluid cognition reflects variation in fluid cognition that is related to the brain MRI and, therefore, indicates the upper limit of Brain Age’s capability in capturing fluid cognition. This is, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. Consequently, if we included Brain Cognition, Brain Age and chronological age in the same model to explain fluid cognition, we would be able to examine the unique effects of Brain Cognition that explain fluid cognition beyond Brain Age and chronological age. These unique effects of Brain Cognition, in turn, would indicate the amount of co-variation between brain MRI and fluid cognition that is missed by Brain Age.”

From Discussion:

“Third, by introducing Brain Cognition,  we showed the extent to which Brain Age indices were not able to capture the variation in fluid cognition that is related to brain MRI. More specifically, using Brain Cognition allowed us to gauge the variation in fluid cognition that is related to the brain MRI, and thereby, to estimate the upper limit of what Brain Age can do. Moreover, by examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age.

From our results, Brain Cognition, especially from certain cognition-prediction models such as the stacked models, has relatively good predictive performance, consistent with previous studies (Dubois et al., 2018; Pat, Wang, Anney, et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022). We then examined Brain Cognition using commonality analyses (Nimon et al., 2008) in multiple regression models having a Brain Age index, chronological age and Brain Cognition as regressors to explain fluid cognition. Similar to Brain Age indices, Brain Cognition exhibited large common effects with chronological age. But more importantly, unlike Brain Age indices, Brain Cognition showed large unique effects, up to around 11%. As explained above, the unique effects of Brain Cognition indicated the amount of co-variation between brain MRI and fluid cognition that was missed by a Brain Age index and chronological age. This missing amount was relatively high, considering that Brain Age and chronological age together explained around 32% of the total variation in fluid cognition. Accordingly, if a Brain Age index was used as a biomarker along with chronological age, we would have missed an opportunity to improve the performance of the model by around one-third of the variation explained.” 

This is a reasonably good paper and the use of a commonality analysis is a nice contribution to understanding variance partitioning across different covariates. I have some comments that I believe the authors ought to address, which mostly relate to clarity and interpretation 

Reviewer #1 Public Review #1

First, from a conceptual point of view, the authors focus exclusively on cognition as a downstream outcome. I would suggest the authors nuance their discussion to provide broader considerations of the utility of their method and on the limits of interpretation of brain age models more generally. 

Thank you for your comments on this issue. 

We now discussed the broader consideration in detail:

(1) the consistency between our findings on fluid cognition and other recent works on brain disorders, 

(2) the difference between studies investigating the utility of Brain Age in explaining cognitive functioning, including ours and others (e.g., Butler et al., 2021; Cole, 2020, 2020; Jirsaraie, Kaufmann, et al., 2023) and those explaining neurological/psychological disorders (e.g., Bashyam et al., 2020; Rokicki et al., 2021)

and 

(3) suggested solutions we and others made to optimise the utility of Brain Age for both cognitive functioning and brain disorders.

From Discussion:

“This discrepancy between the predictive performance of age-prediction models and the utility of Brain Age indices as a biomarker is consistent with recent findings (for review, see Jirsaraie, Gorelik, et al., 2023), both in the context of cognitive functioning (Jirsaraie, Kaufmann, et al., 2023) and neurological/psychological disorders (Bashyam et al., 2020; Rokicki et al., 2021). For instance,  combining different MRI modalities into the prediction models, similar to our stacked models, ocen leads to the highest performance of age prediction models, but does not likely explain the highest variance across different phenotypes, including cognitive functioning and beyond (Jirsaraie, Gorelik, et al., 2023).”

“There is a notable difference between studies investigating the utility of Brain Age in explaining cognitive functioning, including ours and others (e.g., Butler et al., 2021; Cole, 2020, 2020; Jirsaraie, Kaufmann, et al., 2023) and those explaining neurological/psychological disorders (e.g., Bashyam et al., 2020; Rokicki et al., 2021). We consider the former as a normative type of study and the lader as a case-control type of study (Insel et al., 2010; Marquand et al., 2016). Those case-control Brain Age studies focusing on neurological/psychological disorders often build age-prediction models from MRI data of largely healthy participants (e.g., controls in a case-control design or large samples in a population-based design), apply the built age-prediction models to participants without vs. with neurological/psychological disorders and compare Brain Age indices between the two groups. On the one hand, this means that case-control studies treat Brain Age as a method to detect anomalies in the neurological/psychological group (Hahn et al., 2021). On the other hand, this also means that case-control studies have to ignore underfided models when applied prediction models built from largely healthy participants to participants with neurological/psychological disorders (i.e., Brain Age may predict chronological age well for the controls, but not for those with a disorder). On the contrary, our study and other normative studies focusing on cognitive functioning often build age prediction models from MRI data of largely healthy participants and apply the built age prediction models to participants who are also largely healthy. Accordingly, the age prediction models for explaining cognitive functioning in normative studies, while not allowing us to detect group-level anomalies, do not suffer from being under-fided. This unfortunately might limit the generalisability of our study into just the normative type of study. Future work is still needed to test the utility of brain age in the case-control case.”

“Next, researchers should not select age-prediction models based solely on age-prediction performance. Instead, researchers could select age-prediction models that explained phenotypes of interest the best. Here we selected age-prediction models based on a set of features (i.e., modalities) of brain MRI. This strategy was found effective not only for fluid cognition as we demonstrated here, but also for neurological and psychological disorders as shown elsewhere (Jirsaraie, Gorelik, et al., 2023; Rokicki et al., 2021). Rokicki and colleagues (2021), for instance, found that, while integrating across MRI modalities led to age prediction models with the highest age-prediction performance, using only T1 structural MRI gave age-prediction models that were better at classifying Alzheimer’s disease. Similarly, using only cerebral blood flow gave age-prediction models that were better at classifying mild/subjective cognitive impairment, schizophrenia and bipolar disorder. 

As opposed to selecting age-prediction models based on a set of features, researchers could also select age-prediction models based on modelling methods. For instance, Jirsaraie and colleagues (2023) compared gradient tree boosting (GTB) and deep-learning brain network (DBN) algorithms in building age-prediction models. They found GTB to have higher age prediction performance but DBN to have better utility in explaining cognitive functioning. In this case, an algorithm with better utility (e.g., DBN) should be used for explaining a phenotype of interest. Similarly, Bashyam and colleagues (2020) built different DBN-based age-prediction models, varying in age-prediction performance. The DBN models with a higher number of epochs corresponded to higher age-prediction performance. However, DBN-based age-prediction models with a moderate (as opposed to higher or lower) number of epochs were better at classifying Alzheimer’s disease, mild cognitive impairment and schizophrenia. In this case, a model from the same algorithm with better utility (e.g., those DBN with a moderate epoch number) should be used for explaining a phenotype of interest.

Accordingly, this calls for a change in research practice, as recently pointed out by Jirasarie and colleagues (2023, p7), “Despite mounting evidence, there is a persisting assumption across several studies that the most accurate brain age models will have the most potential for detecting differences in a given phenotype of interest”. Future neuroimaging research should aim to build age-prediction models that are not necessarily good at predicting age, but at capturing phenotypes of interest.”

Reviewer #1 Public Review #2

Second, from a methods perspective, there is not a sufficient explanation of the methodological procedures in the current manuscript to fully understand how the stacked regression models were constructed. I would request that the authors provide more information to enable the reader to beUer understand the stacked regression models used to ensure that these models are not overfit. 

Thank you for allowing us an opportunity to clarify our stacked model. We made additional clarification to make this clearer (see below). We wanted to confirm that we did not use test sets to build a stacked model in both lower and higher levels of the Elastic Net models. Test sets were there just for testing the performance of the models.  

From Methods:

“We used nested cross-validation (CV) to build these prediction models (see Figure 7). We first split the data into five outer folds, leaving each outer fold with around 100 participants. This number of participants in each fold is to ensure the stability of the test performance across folds. In each outer-fold CV loop, one of the outer folds was treated as an outer-fold test set, and the rest was treated as an outer-fold training set. Ultimately, looping through the nested CV resulted in a) prediction models from each of the 18 sets of features as well as b) prediction models that drew information across different combinations of the 18 separate sets, known as “stacked models.” We specified eight stacked models: “All” (i.e., including all 18 sets of features),  “All excluding Task FC”, “All excluding Task Contrast”, “Non-Task” (i.e., including only Rest FC and sMRI), “Resting and Task FC”, “Task Contrast and FC”, “Task Contrast” and “Task FC”. Accordingly, there were 26 prediction models in total for both Brain Age and Brain Cognition.

To create these 26 prediction models, we applied three steps for each outer-fold loop. The first step aimed at tuning prediction models for each of 18 sets of features. This step only involved the outer-fold training set and did not involve the outer-fold test set. Here, we divided the outer-fold training set into five inner folds and applied inner-fold CV to tune hyperparameters with grid search. Specifically, in each inner-fold CV, one of the inner folds was treated as an inner-fold validation set, and the rest was treated as an inner-fold training set. Within each inner-fold CV loop, we used the inner-fold training set to estimate parameters of the prediction model with a particular set of hyperparameters and applied the estimated model to the inner-fold validation set. Acer looping through the inner-fold CV, we, then, chose the prediction models that led to the highest performance, reflected by coefficient of determination (R2), on average across the inner-fold validation sets. This led to 18 tuned models, one for each of the 18 sets of features, for each outer fold.

The second step aimed at tuning stacked models. Same as the first step, the second step only involved the outer-fold training set and did not involve the outer-fold test set. Here, using the same outer-fold training set as the first step, we applied tuned models, created from the first step, one from each of the 18 sets of features, resulting in 18 predicted values for each participant. We, then, re-divided this outer-fold training set into new five inner folds. In each inner fold, we treated different combinations of the 18 predicted values from separate sets of features as features to predict the targets in separate “stacked” models. Same as the first step, in each inner-fold CV loop, we treated one out of five inner folds as an inner-fold validation set, and the rest as an inner-fold training set. Also as in the first step, we used the inner-fold training set to estimate parameters of the prediction model with a particular set of hyperparameters from our grid. We tuned the hyperparameters of stacked models using grid search by selecting the models with the highest R2 on average across the inner-fold validation sets. This led to eight tuned stacked models.

The third step aimed at testing the predictive performance of the 18 tuned prediction models from each of the set of features, built from the first step, and eight tuned stacked models, built from the second step. Unlike the first two steps, here we applied the already tuned models to the outer-fold test set. We started by applying the 18 tuned prediction models from each of the sets of features to each observation in the outer-fold test set, resulting in 18 predicted values. We then applied the tuned stacked models to these predicted values from separate sets of features, resulting in eight predicted values. 

To demonstrate the predictive performance, we assessed the similarity between the observed values and the predicted values of each model across outer-fold test sets, using Pearson’s r, coefficient of determination (R2) and mean absolute error (MAE). Note that for R2, we used the sum of squares definition (i.e., R2 \= 1 – (sum of squares residuals/total sum of squares)) per a previous recommendation (Poldrack et al., 2020). We considered the predicted values from the outer-fold test sets of models predicting age or fluid cognition, as Brain Age and Brain Cognition, respectively.”

Author response image 1.

Diagram of the nested cross-validation used for creating predictions for models of each set of features as well as predictions for stacked models. 

Note some previous research, including ours (Tetereva et al., 2022), splits the observations in the outer-fold training set into layer 1 and layer 2 and applies the first and second steps to layers 1 and 2, respectively. Here we decided against this approach and used the same outer-fold training set for both first and second steps in order to avoid potential bias toward the stacked models. This is because, when the data are split into two layers, predictive models built for each separate set of features only use the data from layer 1, while the stacked models use the data from both layers 1 and 2. In practice with large enough data, these two approaches might not differ much, as we demonstrated previously (Tetereva et al., 2022).

Reviewer #1 Public Review #3

Please also provide an indication of the different regression strengths that were estimated across the different models and cross-validation splits. Also, how stable were the weights across splits? 

The focus of this article is on the predictions. Still, it is informative for readers to understand how stable the feature importance (i.e., Elastic Net coefficients) is. To demonstrate the stability of feature importance, we now examined the rank stability of feature importance using Spearman’s ρ (see Figure 4). Specifically, we correlated the feature importance between two prediction models of the same features, used in two different outer-fold test sets. Given that there were five outer-fold test sets, we computed 10 Spearman’s ρ for each prediction model of the same features.  We found Spearman’s ρ to be varied dramatically in both age-prediction (range\=.31-.94) and fluid cognition-prediction (range\=.16-.84) models. This means that some prediction models were much more stable in their feature importance than others. This is probably due to various factors such as a) the collinearity of features in the model, b) the number of features (e.g., 71,631 features in functional connectivity, which were further reduced to 75 PCAs, as compared to 19 features in subcortical volume based on the ASEG atlas), c) the penalisation of coefficients either with ‘Ridge’ or ‘Lasso’ methods, which resulted in reduction as a group of features or selection of a feature among correlated features, respectively, and d) the predictive performance of the models. Understanding the stability of feature importance is beyond the scope of the current article. As mentioned by Reviewer 1, “The predictions can be stable when the coefficients are not,” and we chose to focus on the prediction in the current article.   

Author response image 2.

Stability of feature importance (i.e., Elastic Net Coefficients) of prediction models. Each dot represents rank stability (reflected by Spearman’s ρ) in the feature importance between two prediction models of the same features, used in two different outer-fold test sets. Given that there were five outer-fold test sets, there were 10 Spearman’s ρs for each prediction model.  The numbers to the right of the plots indicate the mean of Spearman’s ρ for each prediction model.  

Reviewer #1 Public Review #4

Please provide more details about the task designs, MRI processing procedures that were employed on this sample in addition to the regression methods and bias correction methods used. For example, there are several different parameterisations of the elastic net, please provide equations to describe the method used here so that readers can easily determine how the regularisation parameters should be interpreted.  

Thank you for the opportunity for us to provide more methodical details.

First, for the task design, we included the following statements:

From Methods:

“HCP-A collected fMRI data from three tasks: Face Name (Sperling et al., 2001), Conditioned Approach Response Inhibition Task (CARIT) (Somerville et al., 2018) and VISual MOTOR (VISMOTOR) (Ances et al., 2009). 

First, the Face Name task (Sperling et al., 2001) taps into episodic memory. The task had three blocks. In the encoding block [Encoding], participants were asked to memorise the names of faces shown. These faces were then shown again in the recall block [Recall] when the participants were asked if they could remember the names of the previously shown faces. There was also the distractor block [Distractor] occurring between the encoding and recall blocks. Here participants were distracted by a Go/NoGo task. We computed six contrasts for this Face Name task: [Encode], [Recall], [Distractor], [Encode vs. Distractor], [Recall vs. Distractor] and [Encode vs. Recall].

Second, the CARIT task (Somerville et al., 2018) was adapted from the classic Go/NoGo task and taps into inhibitory control. Participants were asked to press a budon to all [Go] but not to two [NoGo] shapes. We computed three contrasts for the CARIT task: [NoGo], [Go] and [NoGo vs. Go]. 

Third, the VISMOTOR task (Ances et al., 2009) was designed to test simple activation of the motor and visual cortices. Participants saw a checkerboard with a red square either on the lec or right. They needed to press a corresponding key to indicate the location of the red square. We computed just one contrast for the VISMOTOR task: [Vismotor], which indicates the presence of the checkerboard vs. baseline.” 

Second, for MRI processing procedures, we included the following statements.

From Methods:

“HCP-A provides details of parameters for brain MRI elsewhere (Bookheimer et al., 2019; Harms et al., 2018). Here we used MRI data that were pre-processed by the HCP-A with recommended methods, including the MSMALL alignment (Glasser et al., 2016; Robinson et al., 2018) and ICA-FIX (Glasser et al., 2016) for functional MRI. We used multiple brain MRI modalities, covering task functional MRI (task fMRI), resting-state functional MRI (rsfMRI) and structural MRI (sMRI), and organised them into 19 sets of features.”

“Sets of Features 1-10: Task fMRI contrast (Task Contrast)

Task contrasts reflect fMRI activation relevant to events in each task. Bookheimer and colleagues (2019) provided detailed information about the fMRI in HCP-A. Here we focused on the pre-processed task fMRI Connectivity Informatics Technology Initiative (CIFTI) files with a suffix, “_PA_Atlas_MSMAll_hp0_clean.dtseries.nii.” These CIFTI files encompassed both the cortical mesh surface and subcortical volume (Glasser et al., 2013). Collected using the posterior-to-anterior (PA) phase, these files were aligned using MSMALL (Glasser et al., 2016; Robinson et al., 2018), linear detrended (see hdps://groups.google.com/a/humanconnectome.org/g/hcp-users/c/ZLJc092h980/m/GiihzQAUAwAJ) and cleaned from potential artifacts using ICA-FIX (Glasser et al., 2016). 

To extract Task Contrasts, we regressed the fMRI time series on the convolved task events using a double-gamma canonical hemodynamic response function via FMRIB Software Library (FSL)’s FMRI Expert Analysis Tool (FEAT) (Woolrich et al., 2001). We kept FSL’s default high pass cutoff at 200s (i.e., .005 Hz). We then parcellated the contrast ‘cope’ files, using the Glasser atlas (Gordon et al., 2016) for cortical surface regions and the Freesurfer’s automatic segmentation (aseg) (Fischl et al., 2002) for subcortical regions. This resulted in 379 regions, whose number was, in turn, the number of features for each Task Contrast set of features. “ 

“Sets of Features 11-13: Task fMRI functional connectivity (Task FC)

Task FC reflects functional connectivity (FC ) among the brain regions during each task, which is considered an important source of individual differences (Elliod et al., 2019; Fair et al., 2007; Gradon et al., 2018). We used the same CIFTI file “_PA_Atlas_MSMAll_hp0_clean.dtseries.nii.” as the task contrasts. Unlike Task Contrasts, here we treated the double-gamma, convolved task events as regressors of no interest and focused on the residuals of the regression from each task (Fair et al., 2007). We computed these regressors on FSL, and regressed them in nilearn (Abraham et al., 2014). Following previous work on task FC (Elliod et al., 2019), we applied a highpass at .008 Hz. For parcellation, we used the same atlases as Task Contrast (Fischl et al., 2002; Glasser et al., 2016). We computed Pearson’s correlations of each pair of 379 regions, resulting in a table of 71,631 non-overlapping FC indices for each task. We then applied r-to-z transformation and principal component analysis (PCA) of 75 components (Rasero et al., 2021; Sripada et al., 2019, 2020). Note to avoid data leakage, we conducted the PCA on each training set and applied its definition to the corresponding test set. Accordingly, there were three sets of 75 features for Task FC, one for each task. 

Set of Features 14: Resting-state functional MRI functional connectivity (Rest FC) Similar to Task FC, Rest FC reflects functional connectivity (FC ) among the brain regions, except that Rest FC occurred during the resting (as opposed to task-performing) period. HCPA collected Rest FC from four 6.42-min (488 frames) runs across two days, leading to 26-min long data (Harms et al., 2018). On each day, the study scanned two runs of Rest FC, starting with anterior-to-posterior (AP) and then with posterior-to-anterior (PA) phase encoding polarity. We used the “rfMRI_REST_Atlas_MSMAll_hp0_clean.dscalar.nii” file that was preprocessed and concatenated across the four runs.  We applied the same computations (i.e., highpass filter, parcellation, Pearson’s correlations, r-to-z transformation and PCA) with the Task FC. 

Sets of Features 15-18: Structural MRI (sMRI)

sMRI reflects individual differences in brain anatomy. The HCP-A used an established preprocessing pipeline for sMRI (Glasser et al., 2013). We focused on four sets of features: cortical thickness, cortical surface area, subcortical volume and total brain volume. For cortical thickness and cortical surface area, we used Destrieux’s atlas (Destrieux et al., 2010; Fischl, 2012) from FreeSurfer’s “aparc.stats” file, resulting in 148 regions for each set of features. For subcortical volume, we used the aseg atlas (Fischl et al., 2002) from FreeSurfer’s “aseg.stats” file, resulting in 19 regions. For total brain volume, we had five FreeSurfer-based features: “FS_IntraCranial_Vol” or estimated intra-cranial volume, “FS_TotCort_GM_Vol” or total cortical grey mader volume, “FS_Tot_WM_Vol” or total cortical white mader volume, “FS_SubCort_GM_Vol” or total subcortical grey mader volume and “FS_BrainSegVol_eTIV_Ratio” or ratio of brain segmentation volume to estimated total intracranial volume.”

Third, for regression methods and bias correction methods used, we included the following statements:

From Methods:

“For the machine learning algorithm, we used Elastic Net (Zou & Hastie, 2005). Elastic Net is a general form of penalised regressions (including Lasso and Ridge regression), allowing us to simultaneously draw information across different brain indices to predict one target variable. Penalised regressions are commonly used for building age-prediction models (Jirsaraie, Gorelik, et al., 2023). Previously we showed that the performance of Elastic Net in predicting cognitive abilities is on par, if not better than, many non-linear and morecomplicated algorithms (Pat, Wang, Bartonicek, et al., 2022; Tetereva et al., 2022). Moreover, Elastic Net coefficients are readily explainable, allowing us the ability to explain how our age-prediction and cognition-prediction models made the prediction from each brain feature (Molnar, 2019; Pat, Wang, Bartonicek, et al., 2022) (see below). 

Elastic Net simultaneously minimises the weighted sum of the features’ coefficients. The degree of penalty to the sum of the feature’s coefficients is determined by a shrinkage hyperparameter ‘a’: the greater the a, the more the coefficients shrink, and the more regularised the model becomes. Elastic Net also includes another hyperparameter, ‘ℓ! ratio’, which determines the degree to which the sum of either the squared (known as ‘Ridge’; ℓ! ratio=0) or absolute (known as ‘Lasso’; ℓ! ratio=1) coefficients is penalised (Zou & Hastie, 2005). The objective function of Elastic Net as implemented by sklearn (Pedregosa et al., 2011) is defined as:

where X is the features, y is the target, and b is the coefficient. In our grid search, we tuned two Elastic Net hyperparameters: a using 70 numbers in log space, ranging from .1 and 100, and ℓ!-ratio using 25 numbers in linear space, ranging from 0 and 1.

To understand how Elastic Net made a prediction based on different brain features, we examined the coefficients of the tuned model. Elastic Net coefficients can be considered as feature importance, such that more positive Elastic Net coefficients lead to more positive predicted values and, similarly, more negative Elastic Net coefficients lead to more negative predicted values (Molnar, 2019; Pat, Wang, Bartonicek, et al., 2022). While the magnitude of Elastic Net coefficients is regularised (thus making it difficult for us to interpret the magnitude itself directly), we could still indicate that a brain feature with a higher magnitude weights relatively stronger in making a prediction. Another benefit of Elastic Net as a penalised regression is that the coefficients are less susceptible to collinearity among features as they have already been regularised (Dormann et al., 2013; Pat, Wang, Bartonicek, et al., 2022).

Given that we used five-fold nested cross validation, different outer folds may have different degrees of ‘a’ and ‘ℓ! ratio’, making the final coefficients from different folds to be different. For instance, for certain sets of features, penalisation may not play a big part (i.e., higher or lower ‘a’ leads to similar predictive performance), resulting in different ‘a’ for different folds. To remedy this in the visualisation of Elastic Net feature importance, we refitted the Elastic Net model to the full dataset without spli{ng them into five folds and visualised the coefficients on brain images using Brainspace (Vos De Wael et al., 2020) and Nilern (Abraham et al., 2014) packages. Note, unlike other sets of features, Task FC and Rest FC were modelled acer data reduction via PCA. Thus, for Task FC and Rest FC, we, first, multiplied the absolute PCA scores (extracted from the ‘components_’ attribute of ‘sklearn.decomposition.PCA’) with Elastic Net coefficients and, then, summed the multiplied values across the 75 components, leaving 71,631 ROI-pair indices. “

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Author Response

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

Reviewer #2 (Public Review):

Summary:

In the revised manuscript, the authors aim to investigate brain-wide activation patterns following administration of the anesthetics ketamine and isoflurane, and conduct comparative analysis of these patterns to understand shared and distinct mechanisms of these two anesthetics. To this end, they perform Fos immunohistochemistry in perfused brain sections to label active nuclei, use a custom pipeline to register images to the ABA framework and quantify Fos+ nuclei, and perform multiple complementary analyses to compare activation patterns across groups.

In the latest revision, the authors have made some changes in response to our previous comments on how to fix the analyses. However, the revised analyses were not changed correctly and remain flawed in several fundamental ways.

Critical problems:

(1) Before one can perform higher level analyses such as hiearchal cluster or network hub (or PC) analysis, it is fundamental to validate that you have significant differences of the raw Fos expression values in the first place. First of all, this means showing figures with the raw data (Fos expression levels) in some form in Figures 2 and 3 before showing the higher level analyses in Figures 4 and 5; this is currently switched around. Second and most importantly, when you have a large number of brain areas with large differences in mean values and variance, you need to account for this in a meaningful way. Changing to log values is a step in the right direction for mean values but does not account well for differences in variance. Indeed, considering the large variances in brain areas with high mean values and variance, it is a little difficult to believe that all brain regions, especially brain areas with low mean values, passed corrections for multiple comparisons test. We suggested Z-scores relative to control values for each brain region; this would have accounted for wide differences in mean values and variance, but this was not done. Overall, validation of anesthesia-induced differences in Fos expression levels is not yet shown.

(a) Reordering the figures.

Thank you for your suggestion. We have added Figure 2 (for 201 brain regions) and Figure 2—figure supplement 1 (for 53 brain regions) to demonstrate the statistical differences in raw Fos expression between KET and ISO compared to their respective control groups. These figures specifically present the raw c-Fos expression levels for both KET and ISO in the same brain areas, providing a fundamental basis for the subsequent analyses. Additionally, we have moved the original Figures 4 and 5 to Figures 3 and 4.

(b) Z-score transformation and validation of anesthesia-induced differences in Fos expression.

Thank you for your suggestion. Before multiple comparisons, we transformed the data into log c-Fos density and then performed Z-scores relative to control values for each brain region. Indeed, through Z-score transformation, we have identified a larger number of significantly activated brain regions in Figure 2. The number of brain regions showing significant activation increased by 100 for KET and by 39 for ISO. We have accordingly updated the results section to include these findings in Line 80-181. Besides, we have added the following content in the Statistical Analysis section in Line 489: "…In Figure 2 and Figure 2–figure supplement 1, c-Fos densities in both experimental and control groups were log-transformed. Z-scores were calculated for each brain region by normalizing these log-transformed values against the mean and standard deviation of its respective control group. This involved subtracting the control mean from the experimental value and dividing the result by the control standard deviation. For statistical analysis, Z-scores were compared to a null distribution with a zero mean, and adjustments were made for multiple comparisons using the Benjamini–Hochberg method with a 5% false discovery rate (Q)..…".

Author response image 1.

KET and ISO induced c-Fos expression relative to their respective control group across 201 distinct brain regions. Z-scores represent the normalized c-Fos expression in the KET and ISO groups, calculated against the mean and standard deviation from their respective control groups. Statistical analysis involved the comparison of Z-scores to a null distribution with a zero mean and adjustment for multiple comparisons using the Benjamini–Hochberg method at a 5% false discovery rate (p < 0.05, p < 0.01, **p < 0.001). n = 6, 6, 8, 6 for the home cage, ISO, saline, and KET, respectively. Missing values resulted from zero standard deviations in control groups. Brain regions are categorized into major anatomical subdivisions, as shown on the left side of the graph.

Author response image 2.

KET and ISO induced c-Fos expression relative to their respective control group across 53 distinct brain regions. Z-scores for c-Fos expression in the KET and ISO groups were normalized to the mean and standard deviation of their respective control groups. Statistical analysis involved the comparison of Z-scores to a null distribution with a zero mean and adjustment for multiple comparisons using the Benjamini–Hochberg method at a 5\% false discovery rate (p < 0.05, p < 0.01, **p < 0.001). Brain regions are organized into major anatomical subdivisions, as indicated on the left side of the graph.

(2) Let's assume for a moment that the raw Fos expression analyses indicate significant differences. They used hierarchal cluster analyses as a rationale for examining 53 brain areas in all subsequent analyses of Fos expression following isoflurane versus home cage or ketamine versus saline. Instead, the authors changed to 201 brain areas with no validated rationale other than effectively saying 'we wanted to look at more brain areas'. And then later, when they examined raw Fos expression values in Figures 4 and 5, they assess 43 brain areas for ketamine and 20 brain areas for isoflurane, without any rationale for why choosing these numbers of brain areas. This is a particularly big problem when they are trying to compare effects of isoflurane versus ketamine on Fos expression in these brain areas - they did not compare the same brain areas.

(a) Changing to 201 brain areas with validated rationale.

Thank you for your question. We have revised the original text from “To enhance our analysis of c-Fos expression patterns induced by KET and ISO, we expanded our study to 201 subregions.” to Line 100: "…To enable a more detailed examination and facilitate clearer differentiation and comparison of the effects caused by KET and ISO, we subdivided the 53 brain regions into 201 distinct areas. This approach, guided by the standard mouse atlas available at http://atlas.brain-map.org/atlas, allowed for an in-depth analysis of the responses in various brain regions…". For hierarchal cluster analyses from 53 to 201 brain regions, Line 215: "…To achieve a more granular analysis and better discern the responses between KET and ISO, we expanded our study from the initial 53 brain regions to 201 distinct subregions…"

(b) Compare the same brain areas for KET and ISO and the rationale for why choosing these numbers of brain areas in Figures 3 and 4.

We apologize for the confusion and lack of clarity regarding the selection of brain regions for analysis. In Figure 2 and Figure 2—figure supplement 1, we display the c-Fos expression in the same brain regions affected by KET and ISO. In Figures 3 and 4, we applied a uniform standard to specifically report the brain areas most prominently activated by KET and ISO, respectively. As specified in Line 104: "…Compared to the saline group, KET activated 141 out of a total of 201 brain regions (Figure 2). To further identify the brain regions that are most significantly affected by KET, we calculated Cohen's d for each region to quantify the magnitude of activation and subsequently focused on those regions that had a corrected p-value below 0.05 and effect size in the top 40% (Figure 3, Figure 3—figure supplement 1)…" and Line 142: "…Using the same criteria applied to KET, which involved selecting regions with Cohen's d values in the top 40% of significantly activated areas from Figure 2, we identified 32 key brain regions impacted by ISO (Figure 4, Figure 4—figure supplement 1).…".

Moreover, we illustrate the co-activated brain regions by KET and ISO in Figure 4C. As detailed in Lines 167-180:"…The co-activation of multiple brain regions by KET and ISO indicates that they have overlapping effects on brain functions. Examples of these effects include impacts on sensory processing, as evidenced by the activation of the PIR, ENT 1, and OT2, pointing to changes in sensory perception typical of anesthetics. Memory and cognitive functions are influenced, as indicated by the activation of the subiculum (SUB) 3, dentate gyrus (DG) 4, and RE 5. The reward and motivational systems are engaged, involving the ACB and ventral tegmental area (VTA), signaling the modulation of reward pathways 6. Autonomic and homeostatic control are also affected, as shown by areas like the lateral hypothalamic area (LHA) 7 and medial preoptic area (MPO) 8, emphasizing effects on functions such as feeding and thermoregulation. Stress and arousal responses are impacted through the activation of the paraventricular hypothalamic nucleus (PVH) 10,11 and LC 12. This broad activation pattern highlights the overlap in drug effects and the complexity of brain networks in anesthesia…". Below are the revised Figures 3 and 4.

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(9) Mullican, S. E. et al. GFRAL is the receptor for GDF15 and the ligand promotes weight loss in mice and nonhuman primates. Nat. Med. 23, 1150-1157 (2017). https://doi.org:10.1038/nm.4392

(10) Rasiah, N. P., Loewen, S. P. & Bains, J. S. Windows into stress: a glimpse at emerging roles for CRH(PVN) neurons. Physiol. Rev. 103, 1667-1691 (2023). https://doi.org:10.1152/physrev.00056.2021

(11) Islam, M. T. et al. Vasopressin neurons in the paraventricular hypothalamus promote wakefulness via lateral hypothalamic orexin neurons. Curr. Biol. 32, 3871-3885.e3874 (2022). https://doi.org:10.1016/j.cub.2022.07.020

(12) Ross, J. A. & Van Bockstaele, E. J. The Locus Coeruleus- Norepinephrine System in Stress and Arousal: Unraveling Historical, Current, and Future Perspectives. Front Psychiatry 11, 601519 (2020). https://doi.org:10.3389/fpsyt.2020.601519

Author response image 3.

Brain regions exhibiting significant activation by KET. (A) Fifty-five brain regions exhibited significant KET activation. These were chosen from the 201 regions analyzed in Figure 2, focusing on the top 40\% ranked by effect size among those with corrected p values less than 0.05. Data are presented as mean ± SEM, with p-values adjusted for multiple comparisons (p < 0.05, p < 0.01, **p < 0.001). (B) Representative immunohistochemical staining of brain regions identified in Figure 3A, with control group staining available in Figure 3—figure supplement 1. Scale bar: 200 µm.

Author response image 4.

Brain regions exhibiting significant activation by ISO. (A) Brain regions significantly activated by ISO were initially identified using a corrected p-value below 0.05. From these, the top 40% in effect size (Cohen’s d) were further selected, resulting in 32 key areas. p-values are adjusted for multiple comparisons (p < 0.01, *p < 0.001). (B) Representative immunohistochemical staining of brain regions identified in Figure 4A. Control group staining is available in Figure 4—figure supplement 1. Scale bar: 200 µm. Scale bar: 200 µm. (C) A Venn diagram displays 43 brain regions co-activated by KET and ISO, identified by the adjusted p-values (p < 0.05) for both KET and ISO. CTX: cerebral cortex; CNU: cerebral nuclei; TH: thalamus; HY: hypothalamus; MB: midbrain; HB: hindbrain.

Less critical comments:

(3) The explanation of hierarchical level's in lines 90-95 did not make sense.

We have revised the section that initially stated in lines 90-95, "…Based on the standard mouse atlas available at http://atlas.brain-map.org/, the mouse brain was segmented into nine hierarchical levels, totaling 984 regions. The primary level consists of grey matter, the secondary of the cerebrum, brainstem, and cerebellum, and the tertiary includes regions like the cerebral cortex and cerebellar nuclei, among others, with some regions extending to the 8th and 9th levels. The fifth level comprises 53 subregions, with detailed expression levels and their respective abbreviations presented in Supplementary Figure 2…". Our revised description, now in line 91: "…Building upon the framework established in previous literature, our study categorizes the mouse brain into 53 distinct subregions1…"

(1) Do JP, Xu M, Lee SH, Chang WC, Zhang S, Chung S, Yung TJ, Fan JL, Miyamichi K, Luo L et al: Cell type-specific long-range connections of basal forebrain circuit. Elife 2016, 5.

(4) I am still perplexed by why the authors consider the prelimbic and infralimbic cortex 'neuroendocrine' brain areas in the abstract. In contrast, the prelimbic and infralimbic were described better in the introduction as "associated information processing" areas.

Thank you for bringing this to our attention. We agree that classifying the prelimbic and infralimbic cortex as 'neuroendocrine' in the abstract was incorrect, which was an oversight on our part. In the revised version, as detailed in line 167, we observed an increased number of brain regions showing overlapping activation by both KET and ISO, which is depicted in Figure 4C. This extensive co-activation across various regions makes it challenging to narrowly define the functional classification of each area. Consequently, we have revised the abstract, updating this in line 21: "…KET and ISO both activate brain areas involved in sensory processing, memory and cognition, reward and motivation, as well as autonomic and homeostatic control, highlighting their shared effects on various neural pathways.…".

(5) It looks like overall Fos levels in the control group Home (ISO) are a magnitude (~10-fold) lower than those in the control group Saline (KET) across all regions shown. This large difference seems unlikely to be due to a biologically driven effect and seems more likely to be due to a technical issue, such as differences in staining or imaging between experiments. The authors discuss this issue but did not answer whether the Homecage-ISO experiment or at least the Fos labeling and imaging performed at the same time as for the Saline-Ketamine experiment?

Thank you for highlighting this important point. The c-Fos labeling and imaging for the Home (ISO) and Saline (KET) groups were carried out in separate sessions due to the extensive workload involved in these processes. This study processed a total of 26 brain samples. Sectioning the entire brain of each mouse required approximately 3 hours, yielding 5 slides, with each slide containing 12 to 16 brain sections. We were able to stain and image up to 20 slides simultaneously, typically comprising 2 experimental groups and 2 corresponding control groups. Imaging these 20 slides at 10x magnification took roughly 7 hours, while additional time was required for confocal imaging of specific areas of interest at 20x magnification. Given the complexity of these procedures, to ensure consistency across all experiments, they were conducted under uniform conditions. This included the use of consistent primary and secondary antibody concentrations, incubation times, and imaging parameters such as fixed light intensity and exposure time. Furthermore, in the saline and KET groups, intraperitoneal injections might have evoked pain and stress responses in mice despite four days of pre-experiment acclimation, which could have contributed to the increased c-Fos expression observed. This aspect, along with the fact that procedures were conducted in separate sessions, might have introduced some variations. Thus, we have included a note in our discussion section in Line 353: "…Despite four days of acclimation, including handling and injections, intraperitoneal injections in the saline and KET groups might still elicit pain and stress responses in mice. This point is corroborated by the subtle yet measurable variations in brain states between the home cage and saline groups, characterized by changes in normalized EEG delta/theta power (home cage: 0.05±0.09; saline: -0.03±0.11) and EMG power (home cage: -0.37±0.34; saline: 0.04±0.13), as shown in Figure 1–figure supplement 1. These changes suggest a relative increase in brain activity in the saline group compared to the home cage group, potentially contributing to the higher c-Fos expression. Additionally, despite the use of consistent parameters for c-Fos labeling and imaging across all experiments, the substantial differences observed between the saline and home cage groups might be partly attributed to the fact that the operations were conducted in separate sessions.…"

Reviewer #3 (Public Review):

The present study presents a comprehensive exploration of the distinct impacts of Isoflurane and Ketamine on c-Fos expression throughout the brain. To understand the varying responses across individual brain regions to each anesthetic, the researchers employ principal component analysis (PCA) and c-Fos-based functional network analysis. The methodology employed in this research is both methodical and expansive. Notably, the utilization of a custom software package to align and analyze brain images for c-Fos positive cells stands out as an impressive addition to their approach. This innovative technique enables effective quantification of neural activity and enhances our understanding of how anesthetic drugs influence brain networks as a whole.

The primary novelty of this paper lies in the comparative analysis of two anesthetics, Ketamine and Isoflurane, and their respective impacts on brain-wide c-Fos expression. The study reveals the distinct pathways through which these anesthetics induce loss of consciousness. Ketamine primarily influences the cerebral cortex, while Isoflurane targets subcortical brain regions. This finding highlights the differing mechanisms of action employed by these two anesthetics-a top-down approach for Ketamine and a bottom-up mechanism for Isoflurane. Furthermore, this study uncovers commonly activated brain regions under both anesthetics, advancing our knowledge about the mechanisms underlying general anesthesia.

We are thankful for your positive and insightful comments on our study. Your recognition of the study's methodology and its significance in advancing our understanding of anesthetic mechanisms is greatly valued. By comprehensively mapping c-Fos expression across a wide range of brain regions, our study reveals the distinct and overlapping impacts of these anesthetics on various brain functions, providing a valuable foundation for future research into the mechanisms of general anesthesia, potentially guiding the development of more targeted anesthetic agents and therapeutic strategies. Thus, we are confident that our work will captivate the interest of our readers.

Author Response

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

We sincerely thank the editor and reviewers for their constructive feedback on our manuscript. Based on their recommendations, we've conducted additional experiments, made revisions to the text and figures, and provide a point-by-point response below.

Reviewer #1 (Recommendations for the authors):

1) The lack of behavioral/physiological measures of the depth of anesthesia (ventilation, heart rate, blood pressure, temperature, O2, pain reflexes, etc...) combined with the lack of dose-response and the use of different routes of administration makes the data difficult to interpret. Sure, there is a clear difference in network activation between KET and ISO, but are those effects due to the depth of the anesthesia, the route of administration, and the dose used? The lack of behavioral/physiological measures prevents the identification of brain regions responsible for some of the physiological effects and different effects of anesthetics.

We greatly appreciate the insightful feedback you have provided.

In response to the concerns about anesthesia depth:

a. We recorded EEG and EMG data both before and after drug administration. Supplementary Figure 1 showcases the changes in EEG and EMG power observed 30 minutes post-drug administration, normalized to a 5-minute baseline taken prior to the drug's administration. Notably, no significant differences were detected in the normalized EEG and EMG power between the ISO and KET groups. Given the marked statistical differences observed between the EEG power in the KET and saline groups, and the EMG power in the home cage and ISO groups, we infer that both anesthetics effectively induced a loss of consciousness.

b. We used standard methods and doses for inducing c-Fos expression with anesthetics, as documented in prior studies (Hua, T, et al., Nat Neurosci, 2020; 23(7): 854-868; Jiang-Xie, L F, et al., Neuron, 2019; 102(5): 1053-1065.e4; Lu, J, et al., J Comp Neurol, 2008; 508(4): 648-62). In future research, it might be more optimal to adopt continuous intraperitoneal or intravenous administration of ketamine.

c. Within the scope of our study, while disparities in anesthesia duration might potentially influence the direct statistical comparison of ISO and KET, such disparities wouldn't compromise the identification of brain regions activated by KET or ISO when assessed as distinct stimuli (ISO vs. home cage; KET vs. saline) or in relation to their individual functional network hub node results.

We hope these additions and clarifications adequately address your concerns and enhance the comprehensibility of our data.

2) Under anesthesia there should be an overall reduction of activity, is that the case? There is no mention of significantly downregulated regions. The authors use multiple transformations of the data to interpret the results (%, PC1 values, logarithm) without much explanation or showing the full raw data in Fig 1. It would be helpful to interpret the data to compare the average fos+ neurons in each region between treatment and control for each drug.

Absence of Significantly Downregulated Regions Under Anesthesia: There are two primary reasons for this observation:

a. Our study's sampling time for the home cage, ISO, saline, and KET groups was during Zeitgeber Time (ZT) 6-7.5. During this period, mice in both the home cage and saline groups typically showed reduced spontaneous activity or were in a sleep state. Our Supplementary Figure 1 EEG and EMG data corroborate this, revealing no significant statistical variations in EEG power between the home cage and ISO groups, nor in EMG power between the saline and KET groups.

b. Our immunohistochemical data showed that the total number of c-Fos positive cells in the two control groups was notably lower than in the experimental groups (Saline group vs KET group: 11808±2386 versus 308705±106131, P = 0.006; Home cage vs ISO group: 3371±840 vs 12326±1879, P = 0.001). This is in line with previous studies, like the one by Cirelli C and team, which found minimal c-Fos expression throughout the mouse brain during physiological sleep (Cirelli, C, and G Tononi, Sleep, 2000; 23(4): 453-69). Thus, in our analysis, we did not detect regions with significant downregulation when comparing anesthetized mice with controls.

Interpreting Raw Data from Figure 1: Regarding the average Fos+ neurons:

In Figures 4 and 5, we utilized raw data (c-Fos cell count) to assess cell expression differences across 201 brain regions within each group. Only brain regions that had significant statistical differences after multiple comparison corrections are shown in the figures.

3) I do not understand their interpretation of the PCA analyses. For instance, in Fig 2 they claim that KET is associated with PC1 while ISO is associated with PC2. Looking at the distribution of points it's clear that the KET animals are all grouped at around +2.5 on PC1 and -2.0 on PC2, this means that KET is associated with both PC1 and PC2 to a similar degree (2 to 2.5). Moreover, I'm confused about why they use PCA to represent the animals/group. PCA is a powerful technique to reduce dimensionality and identify groups of variables that may represent the same underlying construct; however, it is not the best way to identify clusters of individuals or groups.

Clarification on PCA Analyses in Figure 2: Thank you for pointing out the ambiguities in our initial presentation of the PCA analyses. We are grateful for the opportunity to address these concerns.

KET and ISO Associations with PC1 and PC2: You rightly observed that KET samples manifest both a positive value on PC1 (around +2.5) and a negative one on PC2 (around -2.0), suggesting that KET has a substantial influence on both principal components. In PCA, a positive score implies a positive association with that component, whereas a negative score suggests a negative association. Contrarily, ISO samples predominantly exhibit values around +2.5 on PC2, with nearly neutral values for PC1, underlining its stronger association with PC2 and lack of significant correlation with PC1. To ensure transparency and clarity, we've adjusted the corresponding descriptions in our manuscript, which can be found on Line 100.

Rationale Behind Using PCA to Represent Animals/Groups: Our initial step was to conduct PCA clustering analysis on the 201 brain regions within both the ISO and KET groups. In the accompanying chart, varying colors denote different brain regions, while distinct shapes represent separate clusters. There wasn't a pronounced distribution pattern within the ISO and KET groups, which led us to adopt the current computational method presented in the paper. This approach was chosen to directly contrast the relative differential expressions between ISO and KET.

We deeply value your feedback, which has steered us toward a clearer and more accurate presentation of our data. We genuinely appreciate your meticulous review.

Author response image 1.

4) The actual metric used for the first PCA is unclear, is it the FOS density in each of the regions (some of those regions are large and consist of many subregions, how does that affect the analysis) is it the %-fos, or normalized cells? The wording describing this is variable causing some confusion. How would looking at these different metrics influence the analysis?

Thank you for raising concerns about the metrics used in our PCA analysis. We recognize the need for clearer exposition and appreciate the opportunity to clarify.

PCA Metrics: The metric for our PCA is calculated by obtaining the ratio of the Fos density within a specific brain region to the global Fos density across the brain. Briefly, this entails dividing the number of Fos-positive cells in a given region by its volume, and then comparing this to the Fos density of the whole brain. The logarithm of this ratio provides our PCA metric. We've elaborated on this in the Materials and Methods section (Lines 401) and enhanced clarity in our revised manuscript, particularly at Line 96.

In Figure 2A, we employed 53 larger, mutually exclusive brain regions based on the reference from the study by Do et al. (eLife, 2016;5:e13214). However, in Figure 3A, we used a more detailed segmentation, incorporating 201 distinct brain areas that are more granular than those in Figure 2A. Notably, the PCA results from both representations were consistent. The rationale behind selecting either the 53 or 201 brain regions can be found in our response to Question 10.

Rationale for Metric Choice: The log ratio of regional c-Fos densities relative to the global brain density was chosen due to:

a. Notable disparities in c-Fos cell expression across the groups.

b. A significant non-normal distribution of density values across animals within the group. Employing the log ratio effectively mitigates the impact of extreme values and outliers, achieving a more standardized data distribution.

We've added PCA plots based on c-Fos densities, depicted in Author response image 2. However, the data dispersion has resulted in a significantly spread-out horizontal scale for these visuals.

Author response image 2.

5) Based on Fig 3 the authors concludes that ISO activates the hypothalamic regions and inhibits the cortex, however, Fig 1 shows neither an activation of the hypothalamus in the ISO nor an inhibition of the cortex when compared to home cage control. If anything it suggests the opposite.

Thank you for your insightful observations regarding the discrepancies between Figures 2 and 3. We believe that when you refer to Figure 1, you are actually referencing Figure 2C.

ISO activation in Hypothalamus: In Figure 2C, we regret the oversight where we inadvertently interchanged the positions of ISO and Saline. When accurately represented, Figure 2C indeed shows that ISO notably activates the periventricular zone (PVZ) and the lateral zone (LZ) of the hypothalamus compared to the home cage group. Moreover, there's a discernible difference in the hypothalamic response between ISO and KET.

ISO's Effect on the Cortex: The main aim of Figure 3 was to highlight the differing responses between ISO and KET in the cortex. Notably, KET demonstrates a positive correlation with PC1 (+7 on PC1), whereas ISO shows a negative association (-3 on PC1). Given that the coefficient of PC1 for the cortical region is positive, it suggests that the cortical areas activated by KET are inhibited by ISO (with KET's distribution around 0 on PC2). However, the divergence between ISO and the home cage is most apparent in PC2, with ISO clusters at +4 and the home cage approximately at -2, suggesting that ISO activates a different set of cortical nuclei. In alignment with this, Figure 2C also illustrates that ISO activates specific cortical areas, such as ILA and PIR, in contrast to the home cage.

Thus, Figure 3 primarily employs PCA to delineate the contrasts between ISO and KET, whereas Figure 2C emphasizes the comparison of each against their respective controls.

6) Control for isoflurane should be air in the induction chamber rather than home cage. It is possible that Fos activation reflects handling/stress pre-anesthesia in the animals, which would increase Fos expression in the stress-related regions such as the BST, striatum (CeA), hypothalamus (PVH) and potentially the LC.

Thank you for emphasizing the importance of an appropriate control for Isoflurane.

In our efforts to minimize the potential impact of stress-induced c-Fos expression, we implemented several precautionary measures. Prior to the experiment, both groups of mice were subjected to handling and acclimatization within the induction chamber over four days. By the day of the experiment, for the mice in the experimental group, we ensured they were comfortable and exhibited no signs of distress or fear—such as cowering or evading. With care, we slowly relocated them to the nearby anesthesia induction chamber. Using 5% ISO, anesthesia was induced promptly, following a meticulously devised protocol to reduce stress impacts on c-Fos expression.

Moreover, existing studies have shown Isoflurane's activation of BST/CeA (Hua, T, et al., Nat Neurosci, 2020, 23: 854-868), PVH (Xu, Z, et al., British Journal of Anaesthesia, 2023, 130: 446-458), and LC (Lu, J, et al., J Comp Neurol, 2008, 508: 648-62), even when using oxygen controls. Such literature supports our findings, indicating that the activation we observed was indeed due to Isoflurane and not purely stress-related.

7) In the Ket network there are a few anticorrelated regions, most of which are amongst the list of the most activated regions, does this mean that the strong correlation results from an overall decreased activation? And if so, is it possible that the ketamine anesthesia was stronger than the isoflurane, causing a more general reduction in activity?

The pronounced correlations observed within the ketamine (KET) network do not signify a generalized decrease in activation. Instead, these correlations reflect significantly enhanced activity in specific regions under KET anesthesia. This amplified correlation is an indication of a more widespread increase in activity, rather than a decrease. These findings are consistent with previous research, which showed that anesthetic doses of ketamine produce patterns of Fos expression in the CNS similar to wakefulness (Lu, J, et al., J Comp Neurol, 2008; 508(4): 648-62).

Regarding the comparative strength of KET versus ISO anesthesia, our electroencephalographic evidence confirms that both agents induce a loss of consciousness. No significant differences were observed in EEG and EMG readings within the first 30 minutes post-administration. In future research, a continuous intravenous or intraperitoneal administration of KET might be a preferable method.

8) Since they have established networks it would be easy and useful to look at how the different regions identified (sleep, pain, neuroendocrine, motor-related, ...) work together to maintain analgesia, are they within the same module? Do they become functionally connected and is this core network of functional connections similar for KET and ISO?

Thank you for your suggestion. In response to your inquiry, we undertook analysis of the core functional networks for KET and ISO, using a set threshold at r>0.82 and P<0.05. For evaluating the modularity of each network, we utilized Newman's spectral community detection algorithm.

(A) The ISO’s core functional network (56 nodes, 372 edges) predominantly divides into two modules with a modularity quotient of 0.345. ISO-active regions include arousal-associated regions (PL, ILA, PVT), analgesia-related (CeA, LC, PB), neuroendocrine function nuclei (TU, PVi, ARH, PVH, SON) as detailed in Figure 5. Notably, ARH and SON weren't incorporated into the core network. Analgesia-associated regions, such as CeA, LC, and PB, reside within module 1, while neuroendocrine nuclei are spread between modules 1 and 2.

(B) In contrast, KET's core functional network (61 nodes, 1820 edges) splits into three distinct modules, but its low modularity quotient (0.06) indicates a lack of clear functional modularization, suggesting denser interconnections among brain regions. Furthermore, functionally-related regions such as arousal (PL, ILA, PVT, DR), analgesia-related (ACA, APN, PAG, LC), and neuroendocrine regulation (PVH, SON),etc., as seen in Figure 4, are distributed across different modules. This distribution may implies that functions like analgesia and neuroendocrine regulation are not governed by simple, linear processes, but arise from complex, overlapping pathways spanning various modules and functional zones.

In summary, the core functional networks of ISO and KET differ, with functionally-related regions spanning multiple modules, reflecting their diverse roles in varied physiological regulations.

Author response image 3.

9) The naming of the function of some of the regions is very much debatable. For instance, PL/ILA are named "sleep-wakefulness regulation" regions in the paper. I can think of many more important functions of the PL/IL including executive functions, behavioral flexibility, and emotional control. It is unclear how the functions of all the regions were attributed. I am not sure that this biased labeling of structure-function is useful to the reports, it may instead suggest wrong conclusions.

Thank you for your thoughtful feedback regarding our classification of the functions of the PL/ILA regions in our manuscript.

We recognize the challenge in accurately defining the functions of brain regions. While there is evidence highlighting the role of PL/ILA in arousal pathways, we also acknowledge their documented roles in executive functions, behavioral flexibility, and emotional control. In response to your comments, we have refined our description, changing "sleep-wakefulness regulation" to "wake-promoting pathways" (see Line: 159, 164).

It's worth noting that many brain regions, including the PL/ILA, have multiple functions. We agree that a single label might not capture the entirety of their roles. To provide a broader perspective, we will add a section in our manuscript that sheds light on the varied functions of these regions (Line: 181).

10) A point of concern and confusion is the number of brain regions analyzed. In the introduction, it is mentioned that 987 brain regions are considered, but this is reduced to 53 selected brain regions in Figure 2, then 201 brain regions in Figure 3, and reduced again to 63 for the network analysis. The rationale for selecting different brain regions is not clear.

For the 987 brain regions: Using the standard mouse atlas available at http://atlas.brain-map.org/, the mouse brain is organized into nine levels. The broadest category is the grey matter, which then progresses to more specific subdivisions, totaling 987 unique regions.

For the 53 brain regions: To effectively understand the activation patterns of ISO and KET, we started with a broad approach, looking at larger brain areas like the thalamus and hypothalamus. This broad view, presented in Figure 2, focuses on the 5th-level brain regions, encompassing 53 primary areas. This methodology is also employed in the study by Do et al. (Elife, 2016; 5: e13214). We have added the rationale for selecting these brain regions in the main text (Line: 92).

Regarding the 201 brain regions in Figures 3, 4, and 5: We delved deeper, examining the 6th-level brain regions, a common granularity in neuroscience research. This detailed view allowed us to highlight specific areas, like the CeA and PVH (Line:129).

Finally, for Figures 6 and 7, we selected 63 regions that were activated by both ISO and KET, as well as regions previously reported to be related to the mechanism of general anesthesia(Leung, L, et al., Progress in neurobiology, 2014; 122: 24-44) (Line: 220). Using these regions, we analyzed the correlation of c-Fos expression, aiming to construct a functional brain network with strong positive connections.

We hope this clarifies our approach and the rationale behind our region selection at each stage of the study. Thank you for your attention to this detail.

11) The statistical analysis does not seem appropriate considering the high number of comparisons. They use simple t-tests without correction for multiple comparisons.

Thank you for pointing out the concern regarding our statistical analysis. In the revised manuscript, we addressed the issue of multiple comparisons correction in our t-tests. We adopted the statistical methods detailed in the papers by Renier, N, et al., Cell, 2016; and Benjamini, Y, and Y Hochberg, 1995. P-values were adjusted for multiple comparisons using the two-stage linear step-up procedure of Benjamini, Krieger, and Yekutieli, with a false discovery rate (FDR) threshold (Q) of 0.05. This approach is now explained in the Materials and Methods section (Line: 434). After this adjustment, the brain regions we initially identified remained statistically significant. Furthermore, we revisited the original immunohistochemical images to confirm the differences in c-Fos cell expression between the experimental and control groups, reinforcing our conclusions.

12) There is no statistical analysis in Fig 2C。

Thank you for bringing to our attention the lack of statistical analysis in Fig 2C. We have now added the relevant statistical data in Supplementary Table 1 and provided annotations in Fig 2C to reflect this.

Reviewer #2

1) The authors report 987 brain regions in the introduction, but I cannot find any analysis that incorporates these or even which regions they are. Very little rationale is provided for the regions included in any of the analyses and numbers range from 53 in Figure 1, to 201 in Figure 3, to 63 in Figure 6. It would help if the authors could first survey Fos+ counts across all regions to identify a subset that is of interest (significantly changed by either condition compared to control) for follow up analysis.

Thank you for your insightful comments on the number of brain regions analyzed in our study.

987 Brain Regions: The reference to 987 brain regions from the standard mouse atlas (http://atlas.brain-map.org/) represents the entire categorization of the mouse brain across nine levels. We recognize that a comprehensive analysis of all these regions would be valuable, but to ensure clarity and depth, we took a focused approach.

Region Selection Rationale:

Figure 2: Concentrated on 5th-level brain regions (53 areas), inspired by methods from Do et al. (eLife, 2016;5:e13214). This provided a broad overview of c-Fos expression differences. Figures 4 and 5: Delved into 6th-level brain regions (201 areas), a common practice in neuroscience for more detailed study. Figure 6: We focused on 63 regions, which encompass not only the regions activated by both ISO and KET but also those previously reported to be associated with the mechanisms of general anesthesia. Methodological Approach: Our region selection was rooted in identifying areas with significant changes under anesthetic conditions compared to controls. This staged approach allowed a targeted analysis of the most affected regions, ensuring robust conclusions.

Enhancements: We've incorporated comparative analyses of activated brain regions at different hierarchical levels in Figures 4 and 5. For clearer comprehension, we’ve added clarifications in the manuscript at Lines: 92, 130, and 220.

2) Different data transformations are used for each analysis. One that is especially confusing is the 'normalization' of brain regions by % of total brain activation for each animal prior to PCA analysis in Figures 2 and 3. This would obscure any global differences in activation and make it unlikely to observe decreases in activation (which I think is likely here) that could be identified using the Fos+ counts after normalizing for region size (ie. Fos+ count / mm3) which is standard practice in such Fos-based activity mapping studies. While PCA can be powerful approach to identify global patterns, the purpose of the analysis in its current form is unclear. It would be more meaningful to show that regional activation patterns (measured as counts/mm3) are on separate PCs by group.

Thank you for your thoughtful comments. We regret any confusion caused by our initial presentation. For the PCA analysis in Figures 2A and 3A, we calculated the ratio of cell density in each brain region to the overall brain density, and then applied a logarithmic transformation to this ratio. Our approach in Figure 2C was to use the proportion of c-Fos cell counts in individual brain regions to the total cell counts throughout the brain. This methodology considers variations in overall c-Fos cell counts across animals, effectively mitigating potential biases due to differential global activation levels across subjects.

Furthermore, our direct comparison of differences in c-Fos cell counts between ISO, KET, and their respective control groups in Figures 4 and 5 addresses your concerns about potential decreases in activation. Notably, we did not identify any brain regions with significant suppression in these figures, which is consistent with the trends observed post-normalization in Figure 2C.

Given your feedback, we conducted another PCA using cell densities for each region (counts/mm3). However, we found significant variability and non-normal distribution of c-Fos density across the groups, leading to extensive data dispersion. Consequently, normalizing the cell counts across regions and then applying a logarithmic transformation before PCA might be more appropriate.

Author response image 4.

Additionally, our exploration of regional activation patterns using PCA analysis for ISO and KET separately, based on the logarithm ratio of the c-Fos density, revealed that there was no distinct clustering feature among the different brain regions (as illustrated in Author response image 5: colors represented distinct brain regions, while the shapes were indicative of different clusters). This observation further suggests that our original statistical approach might be more suitable.

Author response image 5.

3) Critical problem: The authors include a control group for each anesthetic (ketamine vs. saline, isofluorane vs. homecage) but most analyses do not make use of the control groups or directly compare Fos+ counts across the groups. Strictly speaking, they should have compared relative levels of induction by ketamine versus induction by isoflurane using ANOVAs. Instead, each type of induction was separate from the other. This does not account for increased variability in the ketamine versus isoflurane groups. There is no mention in the Statistics section or in Results section that any multiple comparison corrections were used. It appears that the authors only used Students t-test for each region and did not perform any corrections.

We appreciate the reviewer's insights and have addressed your concerns:

Given the pronounced difference in c-Fos cell count expression between the KET and ISO groups, a direct comparison of Fos+ counts may not effectively capture their inherent disparities. To better highlight these distinctions, we used the logarithm ratio of c-Fos density in our PCA analysis (Figure 3), mitigating potential disparities in overall cell counts between samples and emphasizing relative variations. However, in response to your feedback, we've included additional analyses. Author response image 6 depicts the c-Fos density (cells/mm^3) across different brain regions for the home cage, ISO, saline, and KET groups, with regions like the cerebral cortex, cerebral nuclei, thalamus, and others differentiated by shaded backgrounds. Data are represented as mean ± SEM. We performed a one-way ANOVA followed by Tukey’s post hoc test, marking significant differences between ISO and KET with asterisks: P < 0.001, P < 0.01, P < 0.05.

Regarding multiple comparison corrections, we've conducted thorough analyses on the data in Figure 2C and Figures 4, 5, and 6, implementing multiple comparison corrections. The detailed methodology is provided in the “Statistical analysis” section.

Author response image 6.

4) Figures 4 and 5 show brain regions 'significantly activated' following KET or ISO respectively, but again a subset of regions are shown and the stats seem to be t-tests with no multiple comparisons correction. It would help to show these two figures side by side, include the same regions, and keep the y axis ranges similar so the reader can easily compare the 'activation patterns' across the two treatments. Indeed, it looks like KET/Saline induced activation is an order or magnitude or two higher than ISO/Homecage. I would also recommend that this be the first data figure before any other analyses and maybe further analysis could be restricted to regions that are significantly changed in following KET or ISO here.

Thank you for your constructive feedback regarding Figures 4 and 5.

Comparison and Presentation of Figures 4 and 5: We acknowledge your suggestion to present these figures side by side for easier comparison. In the supplementary figure provided in the previous question, we've placed Figures 4 and 5 adjacent to each other, with consistent y-axis ranges, ensuring that readers can make direct comparisons between the activation patterns elicited by KET and ISO.

Statistical Concerns and Region Selection: As mentioned in our previous response, we have conducted multiple comparison corrections on the data presented in Figures 4 and 5. Detailed procedures are elaborated in the “Statistical analysis” section. We believe this approach addresses your concerns regarding the use of t-tests without corrections for multiple comparisons.

Difference in Activation Levels: We observed that the c-Fos activation due to KET is significantly higher than that from ISO. When presented side-by-side using the same scale, ISO activations appear less prominent, potentially mask subtle differences in the activation patterns of ISO, particularly if both KET and ISO showed changes in the same direction in certain brain regions but differed in magnitude. To address this, we used the proportion of c-Fos cell counts in Figure 2C, the logarithm ratio of c-Fos density in Figure 2A and Figure 3. This method emphasizes the relative changes, rather than absolute values, giving a more balanced view of the effects of each treatment.

5) Analyses in Figure 6 and 7 are interesting but again the choice of regions to include is unclear and makes interpreting the results impossible. For example, in Figure 7 it is unclear why the list of regions in bar graphs showing Degree and Betweenness Centrality are not the same even within a single row?

Thank you for your pertinent observation. The choice of brain regions in Figures 6 and 7 was carefully determined based on two main criteria: regions that were significantly activated by ISO or KET within the scope of our study, and those previously reported to be associated with anesthesia mechanisms and sleep-wake regulation.

Regarding your second concern on Figure 7, the discrepancies observed in the x-axes of the bar graphs arise from our methodological approach. We prioritized presenting the top 20% of regions based on their Degree or Betweenness Centrality values. By separately ranking these regions from highest to lowest, the regions presented for each metric inherently differ. This approach was taken to elucidate nodes that consistently emerge as significant across both metrics, thereby highlighting core nodes in the functional network. Were we to use a consistent x-axis without this ranking, it would not only necessitate a more extensive presentation but might also dilute the emphasis on key information. To clarify this methodology and its rationale for our readers, we have expanded upon this in the manuscript at Line 243.

We hope these clarifications address your concerns and facilitate a clearer understanding of our findings.

Reviewer #1 (Recommendations For The Authors):

Minor points

1) In Table 1: the separation of which substructures belong to which brain structure is not clear

2) Line 132 on page 3 seems to repeat the sentence earlier in the paragraph "KET predominantly affects brain regions within the cerebral cortex (CTX), while significantly inhibiting the hypothalamus, midbrain, and hindbrain."

3) Typos

a) Line 99/100 and 130 Central nucleus (CNU) should be cerebral nucleus

b) Comma on line 166

c) Fig. 4D: KET instead of Keta

d) Line 263 "ep"

e) Line 332: 35" "ml (add space)

4) Will data and code be made available?

Thank you for your detailed feedback.

1. We have revised Table 1 to clarify which substructures belong to which brain structures.

2. We acknowledge the redundancy and have now edited line 139 on page 3 to remove the repeated sentence regarding the effects of KET on brain regions.

3. We have addressed the typos you pointed out:

a. The terms "Central nucleus (CNU)" have been corrected to "cerebral nucleus."

b. The comma issue on line 166 has been rectified.

c. In Fig. 4D, we have corrected "Keta" to "KET."

d. We have corrected the typo "ep" on line 263.

e. A space has been added between "35" and "ml" on line 332 as you indicated.

1. Regarding the availability of data and code, we are currently conducting additional analyses related to this study. Once these analyses are completed, we will be more than happy to make the data and code available.

Thank you for assisting us in improving our manuscript.

Reviewer #2 (Recommendations For The Authors):

Minor comments:

6) The term 'whole-brain mapping' in the title suggests that the mapping was performed on 'intact brains' where in fact serial sections were used here. Maybe the authors could change to 'brain-wide mapping' to align better with the study.

Thank you for your insightful comments.

We have revised the title as suggested, changing "whole-brain mapping" to "brain-wide mapping".

7) It is unclear if the mice were kept under anesthesia for the 90-min duration and how the authors monitored the level of sedation. Additionally, if the KET mice were already sedated why were they further sedated with ISO before perfusions and tissue extraction? The methods should be clarified and any potential confounds discussed.

To maintain consistency in the experimental protocol and to reduce stress reactions in the mice, ISO was used before perfusion in all cases. However, this does not affect c-Fos expression as the expression of c-Fos protein starts 20-30 minutes after stimulation (Lara Aparicio, S Y, et al., NeuroSci, 2022; 3(4): 687-702).

We appreciate your guidance in enhancing the clarity of our manuscript.

Reviewer #3 (Recommendations For The Authors):

Recommendation: Minor corrections.

1) The authors should delve deeper into the molecular mechanisms underlying the observed effects, particularly the changes associated with NMDA and GABA receptors. Exploring these mechanisms would provide a more comprehensive understanding of how Ketamine and Isoflurane modulate neural activity and induce anesthesia.

2) The clinical relevance of these findings has not been sufficiently addressed. It would be valuable to elaborate on how the current research outcomes could potentially lead to changes in current anesthesia practices. For instance, identifying the distinct pathways of action for Ketamine and Isoflurane could aid anesthesiologists in selecting the most appropriate anesthetic based on the specific needs of individual patients or surgical procedures.

3) Both Ketamine and Isoflurane have been associated with neurotoxicity. It is important to discuss how the c-Fos activation induced by these anesthetics could contribute, at least partially, to anesthesia-related neurotoxicity. Examining the potential neurotoxic effects would provide a more comprehensive understanding of the risks associated with these anesthetics and aid in the development of safer anesthesia protocols.

Thank you for your valuable suggestions.

Regarding the three points (1, 2, and 3) you've raised, we fully recognize their significance. In the current study, our primary focus was on the differential impacts of Isoflurane and Ketamine on widespread c-Fos expression in the brain. However, we indeed acknowledge the importance of delving deeper into these mechanisms and their clinical relevance. Therefore, we intend to explore these critical issues in greater detail in our future research endeavors.

We appreciate your feedback, which provides constructive guidance for our subsequent research directions.

Author Response:

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

We carefully read through the second-round reviews and the additional reviews. To us, the review process is somewhat unusual and very much dominated by referee 2, who aggressively insists that we mixed up the trigeminal nucleus and inferior olive and that as a consequence our results are meaningless. We think the stance of referee 2 and the focus on one single issue (the alleged mix-up of trigeminal nucleus and inferior olive) is somewhat unfortunate, leaves out much of our findings and we debated at length on how to deal with further revisions. In the end, we decided to again give priority to addressing the criticism of referees 2, because it is hard to go on with a heavily attacked paper without resolving the matter at stake. The following is a summary of, what we did:

Additional experimental work:

(1) We checked if the peripherin-antibody indeed reliably identifies climbing fibers.

To this end, we sectioned the elephant cerebellum and stained sections with the peripherin-antibody. We find: (i) the cerebellar white matter is strongly reactive for peripherin-antibodies, (ii) cerebellar peripherin-antibody staining of has an axonal appearance. (iii) Cerebellar Purkinje cell somata appear to be ensheated by peripherin-antibody staining. (iv) We observed that the peripherin-antibody reactivity gradually decreases from Purkinje cell somata to the pia in the cerebellar molecular layer. This work is shown in our revised Figure 2. All these four features align with the distribution of climbing fibers (which arrive through the white matter, are axons, ensheat Purkinje cell somata, and innervate Purkinje cell proximally not reaching the pia). In line with previous work, which showed similar cerebellar staining patterns in several species (Errante et al. 1998), we conclude that elephant climbing fibers are strongly reactive for peripherin-antibodies.

(2) We delineated the elephant olivo-cerebellar tract.

The strong peripherin-antibody reactivity of elephant climbing fibers enabled us to delineate the elephant olivo-cerebellar tract. We find the elephant olivo-cerebellar tract is a strongly peripherin-antibody reactive, well-delineated fiber tract several millimeters wide and about a centimeter in height. The unstained olivo-cerebellar tract has a greyish appearance. In the anterior regions of the olivo-cerebellar tract, we find that peripherin-antibody reactive fibers run in the dorsolateral brainstem and approach the cerebellar peduncle, where the tract gradually diminishes in size, presumably because climbing fibers discharge into the peduncle. Indeed, peripherin-antibody reactive fibers can be seen entering the cerebellar peduncle. Towards the posterior end of the peduncle, the olivo-cerebellar disappears (in the dorsal brainstem directly below the peduncle. We note that the olivo-cerebellar tract was referred to as the spinal trigeminal tract by Maseko et al. 2013. We think the tract in question cannot be the spinal trigeminal tract for two reasons: (i) This tract is the sole brainstem source of peripherin-positive climbing fibers entering the peduncle/ the cerebellum; this is the defining characteristic of the olivo-cerebellar tract. (ii) The tract in question is much smaller than the trigeminal nerve, disappears posterior to where the trigeminal nerve enters the brainstem (see below), and has no continuity with the trigeminal nerve; the continuity with the trigeminal nerve is the defining characteristic of the spinal trigeminal tract, however.

The anterior regions of the elephant olivo-cerebellar tract are similar to the anterior regions of olivo-cerebellar tract of other mammals in its dorsolateral position and the relation to the cerebellar peduncle. In its more posterior parts, the elephant olivo-cerebellar tract continues for a long distance (~1.5 cm) in roughly the same dorsolateral position and enters the serrated nucleus that we previously identified as the elephant inferior olive. The more posterior parts of the elephant olivo-cerebellar tract therefore differ from the more posterior parts of the olivo-cerebellar tract of other mammals, which follows a ventromedial trajectory towards a ventromedially situated inferior olive. The implication of our delineation of the elephant olivo-cerebellar tract is that we correctly identified the elephant inferior olive.

(3) An in-depth analysis of peripherin-antibody reactivity also indicates that the trigeminal nucleus receives no climbing fiber input.

We also studied the peripherin-antibody reactivity in and around the trigeminal nucleus. We had also noted in the previous submission that the trigeminal nucleus is weakly positive for peripherin, but that the staining pattern is uniform and not the type of axon bundle pattern that is seen in the inferior olive of other mammals. To us, this observation already argued against the presence of climbing fibers in the trigeminal nucleus. We also noted that the myelin stripes of the trigeminal nucleus were peripherin-antibody-negative. In the context of our olivo-cerebellar tract tracing we now also scrutinized the surroundings of the trigeminal nucleus for peripherin-antibody reactivity. We find that the ventral brainstem surrounding the trigeminal nucleus is devoid of peripherin-antibody reactivity. Accordingly, no climbing fibers, (which we have shown to be strongly peripherin-antibody-positive, see our point 1) arrive at the trigeminal nucleus. The absence of climbing fiber input indicates that previous work that identified the (trigeminal) nucleus as the inferior olive (Maseko et al 2013) is unlikely to be correct.

(4) We characterized the entry of the trigeminal nerve into the elephant brain.

To better understand how trigeminal information enters the elephant’s brain, we characterized the entry of the trigeminal nerve. This analysis indicated to us that the trigeminal nerve is not continuous with the olivo-cerebellar tract (the spinal trigeminal tract of Maseko et al. 2013) as previously claimed by Maseko et al. 2013. We show some of this evidence in Referee-Figure 1 below. The reason we think the trigeminal nerve is discontinuous with the olivo-cerebellar tract is the size discrepancy between the two structures. We first show this for the tracing data of Maseko et al. 2013. In the Maseko et al. 2013 data the trigeminal nerve (Referee-Figure 1A, their plate Y) has 3-4 times the diameter of the olivocerebellar tract (the alleged spinal trigeminal tract, Referee-Figure 1B, their plate Z). Note that most if not all trigeminal fibers are thought to continue from the nerve into the trigeminal tract (see our rat data below). We plotted the diameter of the trigeminal nerve and diameter of the olivo-cerebellar (the spinal trigeminal tract according to Maseko et al. 2013) from the Maseko et al. 2013 data (Referee-Figure 1C) and we found that the olivocerebellar tract has a fairly consistent diameter (46 ± 9 mm2, mean ± SD). Statistical considerations and anatomical evidence suggest that the tracing of the trigeminal nerve into the olivo-cerebellar (the spinal trigeminal tract according to Maseko et al. 2013) is almost certainly wrong. The most anterior point of the alleged spinal trigeminal tract has a diameter of 51 mm2 which is more than 15 standard deviations different from the most posterior diameter (194 mm2) of the trigeminal tract. For this assignment to be correct three-quarters of trigeminal nerve fibers would have to spontaneously disappear, something that does not happen in the brain. We also made similar observations in the African elephant Bibi, where the trigeminal nerve (Referee-Figure 1D) is much larger in diameter than the olivocerebellar tract (Referee-Figure 1E). We could also show that the olivocerebellar tract disappears into the peduncle posterior to where the trigeminal nerve enters (Referee-Figure 1F). Our data are very similar to Maseko et al. indicating that their outlining of structures was done correctly. What appears to have been oversimplified, is the assignment of structures as continuous. We also quantified the diameter of the trigeminal nerve and the spinal trigeminal tract in rats (from the Paxinos & Watson atlas; Referee-Figure 1D); as expected we found the trigeminal nerve and spinal trigeminal tract diameters are essentially continuous.

In our hands, the trigeminal nerve does not continue into a well-defined tract that could be traced after its entry. In this regard, it differs both from the olivo-cerebellar tract of the elephant or the spinal trigeminal tract of the rodent, both of which are well delineated. We think the absence of a well-delineated spinal trigeminal tract in elephants might have contributed to the putative tracing error highlighted in our Referee-Figure 1A-C.

We conclude that a size mismatch indicates trigeminal fibers do not run in the olivo-cerebellar tract (the spinal trigeminal tract according to Maseko et al. 2013).

Author response image 1.

The trigeminal nerve is discontinuous with the olivo-cerebellar tract (the spinal trigeminal tract according to Maseko et al. 2013). A, Trigeminal nerve (orange) in the brain of African elephant LAX as delineated by Maseko et al. 2013 (coronal section; their plate Y). B, Most anterior appearance of the spinal trigeminal tract of Maseko et al. 2013 (blue; coronal section; their plate Z). Note the much smaller diameter of the spinal trigeminal tract compared to the trigeminal nerve shown in C, which argues against the continuity of the two structures. Indeed, our peripherin-antibody staining showed that the spinal trigeminal tract of Maseko corresponds to the olivo-cerebellar tract and is discontinuous with the trigeminal nerve. C, Plot of the trigeminal nerve and olivo-cerebellar tracts (the spinal trigeminal tract according to Maseko et al. 2013) diameter along the anterior-posterior axis. The trigeminal nerve is much larger in diameter than the olivocerebellar tract (the spinal trigeminal tract according to Maseko et al. 2013). C, D measurements, for which sections are shown in panels C and D respectively. The olivocerebellar tract (the spinal trigeminal tract according to Maseko et al. 2013) has a consistent diameter; data replotted from Maseko et al. 2013. At mm 25 the inferior olive appears. D, Trigeminal nerve entry in the brain of African elephant Bibi; our data, coronal section, the trigeminal nerve is outlined in orange, note the large diameter. E, Most anterior appearance of the olivo-cerebellar tract in the brain of African elephant Bibi; our data, coronal section, approximately 3 mm posterior to the section shown in A, the olivocerebellar tract is outlined in blue. Note the smaller diameter of the olivo-cerebellar tract compared to the trigeminal nerve, which argues against the continuity of the two structures. F, Plot of the trigeminal nerve and olivo-cerebellar tract diameter along the anterior-posterior axis. The nerve and olivo-cerebellar tract are discontinuous and the trigeminal nerve is much larger in diameter than the olivocerebellar tract (the spinal trigeminal tract according to Maseko et al. 2013); our data. D, E measurements, for which sections are shown in panels D and E respectively. At mm 27 the inferior olive appears. G, In the rat the trigeminal nerve is continuous in size with the spinal trigeminal tract. Data replotted from Paxinos and Watson.

Reviewer 2 (Public Review):

As indicated in my previous review of this manuscript (see above), it is my opinion that the authors have misidentified, and indeed switched, the inferior olivary nuclear complex (IO) and the trigeminal nuclear complex (Vsens). It is this specific point only that I will address in this second review, as this is the crucial aspect of this paper - if the identification of these nuclear complexes in the elephant brainstem by the authors is incorrect, the remainder of the paper does not have any scientific validity.

Comment: We agree with the referee that it is most important to sort out, the inferior olivary nuclear complex (IO) and the trigeminal nuclear complex, respectively.Change: We did additional experimental work to resolve this matter as detailed at the beginning of our response. Specifically, we ascertained that elephant climbing fibers are strongly peripherin-positive. Based on elephant climbing fiber peripherin-reactivity we delineated the elephant olivo-cerebellar tract. We find that the olivo-cerebellar connects to the structure we refer to as inferior olive to the cerebellum (the referee refers to this structure as the trigeminal nuclear complex). We also found that the trigeminal nucleus (the structure the referee refers to as inferior olive) appears to receive no climbing fibers. We provide indications that the tracing of the trigeminal nerve into the olivo-cerebellar tract by Maseko et al. 2023 was erroneous (Author response image 1). These novel findings support our ideas but are very difficult to reconcile with the referee’s partitioning scheme.

The authors, in their response to my initial review, claim that I "bend" the comparative evidence against them. They further claim that as all other mammalian species exhibit a "serrated" appearance of the inferior olive, and as the elephant does not exhibit this appearance, that what was previously identified as the inferior olive is actually the trigeminal nucleus and vice versa. 

For convenience, I will refer to IOM and VsensM as the identification of these structures according to Maseko et al (2013) and other authors and will use IOR and VsensR to refer to the identification forwarded in the study under review. <br /> The IOM/VsensR certainly does not have a serrated appearance in elephants. Indeed, from the plates supplied by the authors in response (Referee Fig. 2), the cytochrome oxidase image supplied and the image from Maseko et al (2013) shows a very similar appearance. There is no doubt that the authors are identifying structures that closely correspond to those provided by Maseko et al (2013). It is solely a contrast in what these nuclear complexes are called and the functional sequelae of the identification of these complexes (are they related to the trunk sensation or movement controlled by the cerebellum?) that is under debate.

Elephants are part of the Afrotheria, thus the most relevant comparative data to resolve this issue will be the identification of these nuclei in other Afrotherian species. Below I provide images of these nuclear complexes, labelled in the standard nomenclature, across several Afrotherian species. 

(A) Lesser hedgehog tenrec (Echinops telfairi) 

Tenrecs brains are the most intensively studied of the Afrotherian brains, these extensive neuroanatomical studies undertaken primarily by Heinz Künzle. Below I append images (coronal sections stained with cresol violet) of the IO and Vsens (labelled in the standard mammalian manner) in the lesser hedgehog tenrec. It should be clear that the inferior olive is located in the ventral midline of the rostral medulla oblongata (just like the rat) and that this nucleus is not distinctly serrated. The Vsens is located in the lateral aspect of the medulla skirted laterally by the spinal trigeminal tract (Sp5). These images and the labels indicating structures correlate precisely with that provide by Künzle (1997, 10.1016, see his Figure 1K,L. Thus, in the first case of a related species, there is no serrated appearance of the inferior olive, the location of the inferior olive is confirmed through connectivity with the superior colliculus (a standard connection in mammals) by Künzle (1997), and the location of Vsens is what is considered to be typical for mammals. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report. 

(B) Giant otter shrew (Potomogale velox) 

The otter shrews are close relatives of the Tenrecs. Below I append images of cresyl violet (left column) and myelin (right column) stained coronal sections through the brainstem with the IO, Vsens and Sp5 labelled as per standard mammalian anatomy. Here we see hints of the serration of the IO as defined by the authors, but we also see many myelin stripes across the IO. Vsens is located laterally and skirted by the Sp5. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report.

(C) Four-toed sengi (Petrodromus tetradactylus) 

The sengis are close relatives of the Tenrecs and otter shrews, these three groups being part of the Afroinsectiphilia, a distinct branch of the Afrotheria. Below I append images of cresyl violet (left column) and myelin (right column) stained coronal sections through the brainstem with the IO, Vsens and Sp5 labelled as per standard mammalian anatomy. Here we see vague hints of the serration of the IO (as defined by the authors), and we also see many myelin stripes across the IO. Vsens is located laterally and skirted by the Sp5. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report. 

(D) Rock hyrax (Procavia capensis) 

The hyraxes, along with the sirens and elephants form the Paenungulata branch of the Afrotheria. Below I append images of cresyl violet (left column) and myelin (right column) stained coronal sections through the brainstem with the IO, Vsens and Sp5 labelled as per the standard mammalian anatomy. Here we see hints of the serration of the IO (as defined by the authors), but we also see evidence of a more "bulbous" appearance of subnuclei of the IO (particularly the principal nucleus), and we also see many myelin stripes across the IO. Vsens is located laterally and skirted by the Sp5. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report. 

(E) West Indian manatee (Trichechus manatus) 

The sirens are the closest extant relatives of the elephants in the Afrotheria. Below I append images of cresyl violet (top) and myelin (bottom) stained coronal sections (taken from the University of Wisconsin-Madison Brain Collection, https://brainmuseum.org, and while quite low in magnification they do reveal the structures under debate) through the brainstem with the IO, Vsens and Sp5 labelled as per standard mammalian anatomy. Here we see the serration of the IO (as defined by the authors). Vsens is located laterally and skirted by the Sp5. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report.

These comparisons and the structural identification, with which the authors agree as they only distinguish the elephants from the other Afrotheria, demonstrate that the appearance of the IO can be quite variable across mammalian species, including those with a close phylogenetic affinity to the elephants. Not all mammal species possess a "serrated" appearance of the IO. Thus, it is more than just theoretically possible that the IO of the elephant appears as described prior to this study. 

So what about elephants? Below I append a series of images from coronal sections through the African elephant brainstem stained for Nissl, myelin, and immunostained for calretinin. These sections are labelled according to standard mammalian nomenclature. In these complete sections of the elephant brainstem, we do not see a serrated appearance of the IOM (as described previously and in the current study by the authors). Rather the principal nucleus of the IOM appears to be bulbous in nature. In the current study, no image of myelin staining in the IOM/VsensR is provided by the authors. However, in the images I provide, we do see the reported myelin stripes in all stains - agreement between the authors and reviewer on this point. The higher magnification image to the bottom left of the plate shows one of the IOM/VsensR myelin stripes immunostained for calretinin, and within the myelin stripes axons immunopositive for calretinin are seen (labelled with an arrow). The climbing fibres of the elephant cerebellar cortex are similarly calretinin immunopositive (10.1159/000345565). In contrast, although not shown at high magnification, the fibres forming the Sp5 in the elephant (in the Maseko description, unnamed in the description of the authors) show no immunoreactivity to calretinin. 

Comment: We appreciate the referee’s additional comments. We concede the possibility that some relatives of elephants have a less serrated inferior olive than most other mammals. We maintain, however, that the elephant inferior olive (our Figure 1J) has the serrated appearance seen in the vast majority of mammals.

Change: None.

Peripherin Immunostaining 

In their revised manuscript the authors present immunostaining of peripherin in the elephant brainstem. This is an important addition (although it does replace the only staining of myelin provided by the authors which is unusual as the word myelin is in the title of the paper) as peripherin is known to specifically label peripheral nerves. In addition, as pointed out by the authors, peripherin also immunostains climbing fibres (Errante et al., 1998). The understanding of this staining is important in determining the identification of the IO and Vsens in the elephant, although it is not ideal for this task as there is some ambiguity. Errante and colleagues (1998; Fig. 1) show that climbing fibres are peripherin-immunopositive in the rat. But what the authors do not evaluate is the extensive peripherin staining in the rat Sp5 in the same paper (Errante et al, 1998, Fig. 2). The image provided by the authors of their peripherin immunostaining (their new Figure 2) shows what I would call the Sp5 of the elephant to be strongly peripherin immunoreactive, just like the rat shown in Errant et al (1998), and more over in the precise position of the rat Sp5! This makes sense as this is where the axons subserving the "extraordinary" tactile sensitivity of the elephant trunk would be found (in the standard model of mammalian brainstem anatomy). Interestingly, the peripherin immunostaining in the elephant is clearly lamellated...this coincides precisely with the description of the trigeminal sensory nuclei in the elephant by Maskeo et al (2013) as pointed out by the authors in their rebuttal. Errante et al (1998) also point out peripherin immunostaining in the inferior olive, but according to the authors this is only "weakly present" in the elephant IOM/VsensR. This latter point is crucial. Surely if the elephant has an extraordinary sensory innervation from the trunk, with 400 000 axons entering the brain, the VsensR/IOM should be highly peripherin-immunopositive, including the myelinated axon bundles?! In this sense, the authors argue against their own interpretation - either the elephant trunk is not a highly sensitive tactile organ, or the VsensR is not the trigeminal nuclei it is supposed to be. 

Comment: We made sure that elephant climbing fibers are strongly peripherin-positive (our revised Figure 2). As we noted in already our previous ms, we see weak diffuse peripherin-reactivity in the trigeminal nucleus (the inferior olive according to the referee), but no peripherin-reactive axon bundles (i.e. climbing fibers) that are seen in the inferior olive of other species. We also see no peripherin-reactive axon bundles (i.e. the olivo-cerebellar tract) arriving in the trigeminal nucleus as the tissue surrounding the trigeminal nucleus is devoid of peripherin-reactivity. Again, this finding is incompatible with the referee’s ideas. As far as we can tell, the trigeminal fibers are not reactive for peripherin in the elephant, i.e. we did not observe peripherin-reactivity very close to the nerve entry, but unfortunately, we did not stain for peripherin-reactivity into the nerve. As the referee alludes to the absence of peripherin-reactivity in the trigeminal tract is a difference between rodents and elephants.

Change: Our novel Figure 2.

Summary: 

(1) Comparative data of species closely related to elephants (Afrotherians) demonstrates that not all mammals exhibit the "serrated" appearance of the principal nucleus of the inferior olive. 

(2) The location of the IO and Vsens as reported in the current study (IOR and VsensR) would require a significant, and unprecedented, rearrangement of the brainstem in the elephants independently. I argue that the underlying molecular and genetic changes required to achieve this would be so extreme that it would lead to lethal phenotypes. Arguing that the "switcheroo" of the IO and Vsens does occur in the elephant (and no other mammals) and thus doesn't lead to lethal phenotypes is a circular argument that cannot be substantiated. 

(3) Myelin stripes in the subnuclei of the inferior olivary nuclear complex are seen across all related mammals as shown above. Thus, the observation made in the elephant by the authors in what they call the VsensR, is similar to that seen in the IO of related mammals, especially when the IO takes on a more bulbous appearance. These myelin stripes are the origin of the olivocerebellar pathway, and are indeed calretinin immunopositive in the elephant as I show. 

(4) What the authors see aligns perfectly with what has been described previously, the only difference being the names that nuclear complexes are being called. But identifying these nuclei is important, as any functional sequelae, as extensively discussed by the authors, is entirely dependent upon accurately identifying these nuclei. 

(4) The peripherin immunostaining scores an own goal - if peripherin is marking peripheral nerves (as the authors and I believe it is), then why is the VsensR/IOM only "weakly positive" for this stain? This either means that the "extraordinary" tactile sensitivity of the elephant trunk is non-existent, or that the authors have misinterpreted this staining. That there is extensive staining in the fibre pathway dorsal and lateral to the IOR (which I call the spinal trigeminal tract), supports the idea that the authors have misinterpreted their peripherin immunostaining.

(5) Evolutionary expediency. The authors argue that what they report is an expedient way in which to modify the organisation of the brainstem in the elephant to accommodate the "extraordinary" tactile sensitivity. I disagree. As pointed out in my first review, the elephant cerebellum is very large and comprised of huge numbers of morphologically complex neurons. The inferior olivary nuclei in all mammals studied in detail to date, give rise to the climbing fibres that terminate on the Purkinje cells of the cerebellar cortex. It is more parsimonious to argue that, in alignment with the expansion of the elephant cerebellum (for motor control of the trunk), the inferior olivary nuclei (specifically the principal nucleus) have had additional neurons added to accommodate this cerebellar expansion. Such an addition of neurons to the principal nucleus of the inferior olive could readily lead to the loss of the serrated appearance of the principal nucleus of the inferior olive, and would require far less modifications in the developmental genetic program that forms these nuclei. This type of quantitative change appears to be the primary way in which structures are altered in the mammalian brainstem. 

Comment: We still disagree with the referee. We note that our conclusions rest on the analysis of 8 elephant brainstems, which we sectioned in three planes and stained with a variety of metabolic and antibody stains and in which assigned two structures (the inferior olive and the trigeminal nucleus). Most of the evidence cited by the referee stems from a single paper, in which 147 structures were identified based on the analysis of a single brainstem sectioned in one plane and stained with a limited set of antibodies. Our synopsis of the evidence is the following.

(1) We agree with the referee that concerning brainstem position our scheme of a ventromedial trigeminal nucleus and a dorsolateral inferior olive deviates from the usual mammalian position of these nuclei (i.e. a dorsolateral trigeminal nucleus and a ventromedial inferior olive).

(2) Cytoarchitectonics support our partitioning scheme. The compact cellular appearance of our ventromedial trigeminal nucleus is characteristic of trigeminal nuclei. The serrated appearance of our dorsolateral inferior olive is characteristic of the mammalian inferior olive; we acknowledge that the referee claims exceptions here. To our knowledge, nobody has described a mammalian trigeminal nucleus with a serrated appearance (which would apply to the elephant in case the trigeminal nucleus is situated dorsolaterally).

(3) Metabolic staining (Cyto-chrome-oxidase reactivity) supports our partitioning scheme. Specifically, our ventromedial trigeminal nucleus shows intense Cyto-chrome-oxidase reactivity as it is seen in the trigeminal nuclei of trigeminal tactile experts.

(4) Isomorphism. The myelin stripes on our ventromedial trigeminal nucleus are isomorphic to trunk wrinkles. Isomorphism is a characteristic of somatosensory brain structures (barrel, barrelettes, nose-stripes, etc) and we know of no case, where such isomorphism was misleading.

(5) The large-scale organization of our ventromedial trigeminal nuclei in anterior-posterior repeats is characteristic of the mammalian trigeminal nuclei. To our knowledge, no such organization has ever been reported for the inferior olive.

(6) Connectivity analysis supports our partitioning scheme. According to our delineation of the elephant olivo-cerebellar tract, our dorsolateral inferior olive is connected via peripherin-positive climbing fibers to the cerebellum. In contrast, our ventromedial trigeminal nucleus (the referee’s inferior olive) is not connected via climbing fibers to the cerebellum.

Change: As discussed, we advanced further evidence in this revision. Our partitioning scheme (a ventromedial trigeminal nucleus and a dorsolateral inferior olive) is better supported by data and makes more sense than the referee’s suggestion (a dorsolateral trigeminal nucleus and a ventromedial inferior olive). It should be published.

Reviewer #3 (Public Review):

Summary: 

The study claims to investigate trunk representations in elephant trigeminal nuclei located in the brainstem. The researchers identify large protrusions visible from the ventral surface of the brainstem, which they examined using a range of histological methods. However, this ventral location is usually where the inferior olivary complex is found, which challenges the author's assertions about the nucleus under analysis. They find that this brainstem nucleus of elephants contains repeating modules, with a focus on the anterior and largest unit which they define as the putative nucleus principalis trunk module of the trigeminal. The nucleus exhibits low neuron density, with glia outnumbering neurons significantly. The study also utilizes synchrotron X-ray phase contrast tomography to suggest that myelin-stripe-axons traverse this module. The analysis maps myelin-rich stripes in several specimens and concludes that based on their number and patterning that they likely correspond with trunk folds; however this conclusion is not well supported if the nucleus has been misidentified. 

Comment: The referee provides a summary of our work. The referee also notes that the correct identification of the trigeminal nucleus is critical to the message of our paper.

Change: In line with these assessments we focused our revision efforts on the issue of trigeminal nucleus identification, please see our introductory comments and our response to Referee 2.

Strengths: 

The strength of this research lies in its comprehensive use of various anatomical methods, including Nissl staining, myelin staining, Golgi staining, cytochrome oxidase labeling, and synchrotron X-ray phase contrast tomography. The inclusion of quantitative data on cell numbers and sizes, dendritic orientation and morphology, and blood vessel density across the nucleus adds a quantitative dimension. Furthermore, the research is commendable for its high-quality and abundant images and figures, effectively illustrating the anatomy under investigation.

Comment: We appreciate this positive assessment.

Change: None

Weaknesses: 

While the research provides potentially valuable insights if revised to focus on the structure that appears to be inferior olivary nucleus, there are certain additional weaknesses that warrant further consideration. First, the suggestion that myelin stripes solely serve to separate sensory or motor modules rather than functioning as an "axonal supply system" lacks substantial support due to the absence of information about the neuronal origins and the termination targets of the axons. Postmortem fixed brain tissue limits the ability to trace full axon projections. While the study acknowledges these limitations, it is important to exercise caution in drawing conclusions about the precise role of myelin stripes without a more comprehensive understanding of their neural connections. 

Comment: We understand these criticisms and the need for cautious interpretation. As we noted previously, we think that the Elife-publishing scheme, where critical referee commentary is published along with our ms, will make this contribution particularly valuable.

Change: Our additional efforts to secure the correct identification of the trigeminal nucleus.

Second, the quantification presented in the study lacks comparison to other species or other relevant variables within the elephant specimens (i.e., whole brain or brainstem volume). The absence of comparative data to different species limits the ability to fully evaluate the significance of the findings. Comparative analyses could provide a broader context for understanding whether the observed features are unique to elephants or more common across species. This limitation in comparative data hinders a more comprehensive assessment of the implications of the research within the broader field of neuroanatomy. Furthermore, the quantitative comparisons between African and Asian elephant specimens should include some measure of overall brain size as a covariate in the analyses. Addressing these weaknesses would enable a richer interpretation of the study's findings. 

Comment: We understand, why the referee asks for additional comparative data, which would make our study more meaningful. We note that we already published a quantitative comparison of African and Asian elephant facial nuclei (Kaufmann et al. 2022). The quantitative differences between African and Asian elephant facial nuclei are similar in magnitude to what we observed here for the trigeminal nucleus, i.e. African elephants have about 10-15% more facial nucleus neurons than Asian elephants. The referee also notes that data on overall elephant brain size might be important for interpreting our data. We agree with this sentiment and we are preparing a ms on African and Asian elephant brain size. We find – unexpectedly given the larger body size of African elephants – that African elephants have smaller brains than Asian elephants. The finding might imply that African elephants, which have more facial nucleus neurons and more trigeminal nucleus trunk module neurons, are neurally more specialized in trunk control than Asian elephants.

Change: We are preparing a further ms on African and Asian elephant brain size, a first version of this work has been submitted.

Reviewer #4 (Public Review): 

Summary: 

The authors report a novel isomorphism in which the folds of the elephant trunk are recognizably mapped onto the principal sensory trigeminal nucleus in the brainstem. Further, they identifiy the enlarged nucleus as being situated in this species in an unusual ventral midline position. 

Comment: The referee summarizes our work.

Change: None.

Strengths: 

The identity of the purported trigeminal nucleus and the isomorphic mapping with the trunk folds is supported by multiple lines of evidence: enhanced staining for cytochrome oxidase, an enzyme associated with high metabolic activity; dense vascularization, consistent with high metabolic activity; prominent myelinated bundles that partition the nucleus in a 1:1 mapping of the cutaneous folds in the trunk periphery; near absence of labeling for the anti-peripherin antibody, specific for climbing fibers, which can be seen as expected in the inferior olive; and a high density of glia.

Comment: The referee again reviews some of our key findings.

Change: None. 

Weaknesses: 

Despite the supporting evidence listed above, the identification of the gross anatomical bumps, conspicuous in the ventral midline, is problematic. This would be the standard location of the inferior olive, with the principal trigeminal nucleus occupying a more dorsal position. This presents an apparent contradiction which at a minimum needs further discussion. Major species-specific specializations and positional shifts are well-documented for cortical areas, but nuclear layouts in the brainstem have been considered as less malleable. 

Comment: The referee notes that our discrepancy with referee 2, needs to be addressed with further evidence and discussion, given the unusual position of both inferior olive and trigeminal nucleus in the partitioning scheme and that the mammalian brainstem tends to be positionally conservative. We agree with the referee. We note that – based on the immense size of the elephant trigeminal ganglion (50 g), half the size of a monkey brain – it was expected that the elephant trigeminal nucleus ought to be exceptionally large.

Change: We did additional experimental work to resolve this matter: (i) We ascertained that elephant climbing fibers are strongly peripherin-positive. (ii) Based on elephant climbing fiber peripherin-reactivity we delineated the elephant olivo-cerebellar tract. We find that the olivo-cerebellar connects to the structure we refer to as inferior olive to the cerebellum. (iii) We also found that the trigeminal nucleus (the structure the referee refers to as inferior olive) appears to receive no climbing fibers. (iv) We provide indications that the tracing of the trigeminal nerve into the olivo-cerebellar tract by Maseko et al. 2023 was erroneous (Referee-Figure 1). These novel findings support our ideas.

Reviewer #5 (Public Review): 

After reading the manuscript and the concerns raised by reviewer 2 I see both sides of the argument - the relative location of trigeminal nucleus versus the inferior olive is quite different in elephants (and different from previous studies in elephants), but when there is a large disproportionate magnification of a behaviorally relevant body part at most levels of the nervous system (certainly in the cortex and thalamus), you can get major shifting in location of different structures. In the case of the elephant, it looks like there may be a lot of shifting. Something that is compelling is that the number of modules separated but the myelin bands correspond to the number of trunk folds which is different in the different elephants. This sort of modular division based on body parts is a general principle of mammalian brain organization (demonstrated beautifully for the cuneate and gracile nucleus in primates, VP in most of species, S1 in a variety of mammals such as the star nosed mole and duck-billed platypus). I don't think these relative changes in the brainstem would require major genetic programming - although some surely exists. Rodents and elephants have been independently evolving for over 60 million years so there is a substantial amount of time for changes in each l lineage to occur.

I agree that the authors have identified the trigeminal nucleus correctly, although comparisons with more out groups would be needed to confirm this (although I'm not suggesting that the authors do this). I also think the new figure (which shows previous divisions of the brainstem versus their own) allows the reader to consider these issues for themselves. When reviewing this paper, I actually took the time to go through atlases of other species and even look at some of my own data from highly derived species. Establishing homology across groups based only on relative location is tough especially when there appears to be large shifts in relative location of structures. My thoughts are that the authors did an extraordinary amount of work on obtaining, processing and analyzing this extremely valuable tissue. They document their work with images of the tissue and their arguments for their divisions are solid. I feel that they have earned the right to speculate - with qualifications - which they provide. 

Comment: The referee summarizes our work and appears to be convinced by the line of our arguments. We are most grateful for this assessment. We add, again, that the skeptical assessment of referee 2 will be published as well and will give the interested reader the possibility to view another perspective on our work.

Change: None. 

Recommendations for the authors: 

Reviewer #1 (Recommendations For The Authors):

With this manuscript being virtually identical to the previous version, it is possible that some of the definitive conclusions about having identified the elephant trigeminal nucleus and trunk representation should be moderated in a more nuanced manner, especially given the careful and experienced perspective from reviewers with first hand knowledge elephant neuroanatomy.

Comment: We agree that both our first and second revisions were very much centered on the debate of the correct identification of the trigeminal nucleus and that our ms did not evolve as much in other regards. This being said we agree with Referee 2 that we needed to have this debate. We also think we advanced important novel data in this context (the delineation of elephant olivo-cerebellar tract through the peripherin-antibody).

Changes: Our revised Figure 2. 

The peripherin staining adds another level of argument to the authors having identified the trigeminal brainstem instead of the inferior olive, if differential expression of peripherin is strong enough to distinguish one structure from the other.

Comment: We think we showed too little peripherin-antibody staining in our previous revision. We have now addressed this problem.

Changes: Our revised Figure 2, i.e. the delineation of elephant olivo-cerebellar tract through the peripherin-antibody).

There are some minor corrections to be made with the addition of Fig. 2., including renumbering the figures in the manuscript (e.g., 406, 521). 

I continue to appreciate this novel investigation of the elephant brainstem and find it an interesting and thorough study, with the use of classical and modern neuroanatomical methods.

Comment: We are thankful for this positive assessment.

Reviewer #2 (Recommendations For The Authors):

I do realise the authors are very unhappy with me and the reviews I have submitted. I do apologise if feelings have been hurt, and I do understand the authors put in a lot of hard work and thought to develop what they have; however, it is unfortunate that the work and thoughts are not correct. Science is about the search for the truth and sometimes we get it wrong. This is part of the scientific process and why most journals adhere to strict review processes of scientific manuscripts. As I said previously, the authors can use their data to write a paper describing and quantifying Golgi staining of neurons in the principal olivary nucleus of the elephant that should be published in a specialised journal and contextualised in terms of the motor control of the trunk and the large cerebellum of the elephant. 

Comment: We appreciate the referee’s kind words. Also, no hard feelings from our side, this is just a scientific debate. In our experience, neuroanatomical debates are resolved by evidence and we note that we provide evidence strengthening our identification of the trigeminal nucleus and inferior olive. As far as we can tell from this effort and the substantial evidence accumulated, the referee is wrong.

Reviewer #4 (Recommendations For The Authors):

As a new reviewer, I have benefited from reading the previous reviews and Author response, even while having several new comments to add. 

(1) The identification of the inferior olive and trigeminal nuclei is obviously center stage. An enlargement of the trigeminal nuclei is not necessarily problematic, given the published reports on the dramatic enlargement of the trigeminal nerve (Purkart et al., 2022). At issue is the conspicuous relocation of the trigeminal nuclei that is being promoted by Reveyaz et al. Conspicuous rearrangements are not uncommon; for example, primary sensory cortical fields in different species (fig. 1 in H.H.A. Oelschlager for dolphins; S. De Vreese et al. (2023) for cetaceans, L. Krubitzer on various species, in the context of evolution). The difficult point here concerns what looks like a rather conspicuous gross anatomical rearrangement, in BRAINSTEM - the assumption being that the brainstem bauplan is going to be specifically conservative and refractory to gross anatomical rearrangement. 

Comment: We agree with the referee that the brainstem rearrangements are unexpected. We also think that the correct identification of nuclei needs to be at the center of our revision efforts.

Change: Our revision provided further evidence (delineation of the olivo-cerebellar tract, characterization of the trigeminal nerve entry) about the identity of the nuclei we studied.

Why would a major nucleus shift to such a different location? and how? Can ex vivo DTI provide further support of the correct identification? Is there other "disruption" in the brainstem? What occupies the traditional position of the trigeminal nuclei? An atlas-equivalent coronal view of the entire brainstem would be informative. The Authors have assembled multiple criteria to support their argument that the ventral "bumps" are in fact a translocated trigeminal principal nucleus: enhanced CO staining, enhanced vascularization, enhanced myelination (via Golgi stains and tomography), very scant labeling for a climbing fiber specific antibody ( anti-peripherin), vs. dense staining of this in the alternative structure that they identify as IO; and a high density of glia. Admittedly, this should be sufficient, but the proposed translocation (in the BRAINSTEM) is sufficiently startling that this is arguably NOT sufficient. <br /> The terminology of "putative" is helpful, but a more cogent presentation of the results and more careful discussion might succeed in winning over at least some of a skeptical readership. 

Comment: We do not know, what led to the elephant brainstem rearrangements we propose. If the trigeminal nuclei had expanded isometrically in elephants from the ancestral pattern, one would have expected a brain with big lateral bumps, not the elephant brain with its big ventromedial bumps. We note, however, that very likely the expansion of the elephant trigeminal nuclei did not occur isometrically. Instead, the neural representation of the elephant nose expanded dramatically and in rodents the nose is represented ventromedially in the brainstem face representation. Thus, we propose a ‘ventromedial outgrowth model’ according to which the elephant ventromedial trigeminal bumps result from a ventromedially direct outgrowth of the ancestral ventromedial nose representation.

We advanced substantially more evidence to support our partitioning scheme, including the delineation of the olivo-cerebellar tract based on peripherin-reactivity. We also identified problems in previous partitioning schemes, such as the claim that the trigeminal nerve continues into the ~4x smaller olivocerebellar tract (Referee-Figure 1C, D); we think such a flow of fibers, (which is also at odds with peripherin-antibody-reactivity and the appearance of nerve and olivocerebellar tract), is highly unlikely if not physically impossible. With all that we do not think that we overstate our case in our cautiously presented ms.

Change: We added evidence on the identification of elephant trigeminal nuclei and inferior olive.

(2) Role of myelin. While the photos of myelin are convincing, it would be nice to have further documentation. Gallyas? Would antibodies to MBP work? What is the myelin distribution in the "standard" trigeminal nuclei (human? macaque or chimpanzee?). What are alternative sources of the bundles? Regardless, I think it would be beneficial to de-emphasize this point about the role of myelin in demarcating compartments. <br /> I would in fact suggest an alternative (more neutral) title that might highlight instead the isomorphic feature; for example, "An isomorphic representation of Trunk folds in the Elephant Trigeminal Nucleus." The present title stresses myelin, but figure 1 already focuses on CO. Additionally, the folds are actually mentioned almost in passing until later in the manuscript. I recommend a short section on these at the beginning of the Results to serve as a useful framework.

Here I'm inclined to agree with the Reviewer, that the Authors' contention that the myelin stipes serve PRIMARILY to separate trunk-fold domains is not particularly compelling and arguably a distraction. The point can be made, but perhaps with less emphasis. After all, the fact that myelin has multiple roles is well-established, even if frequently overlooked. In addition, the Authors might make better use of an extensive relevant literature related to myelin as a compartmental marker; for example, results and discussion in D. Haenelt....N. Weiskopf (eLife, 2023), among others. Another example is the heavily myelinated stria of Gennari in primate visual cortex, consisting of intrinsic pyramidal cell axons, but where the role of the myelination has still not been elucidated. 

Comment: (1) Documentation of myelin. We note that we show further identification of myelinated fibers by the fluorescent dye fluomyelin in Figure 4B. We also performed additional myelin stains as the gold-myelin stain after the protocol of Schmued (Referee-Figure 2). In the end, nothing worked quite as well to visualize myelin-stripes as the bright-field images shown in Figure 4A and it is only the images that allowed us to match myelin-stripes to trunk folds. Hence, we focus our presentation on these images.

(2) Title: We get why the referee envisions an alternative title. This being said, we would like to stick with our current title, because we feel it highlights the major novelty we discovered.

(3) We agree with many of the other comments of the referee on myelin phenomenology. We missed the Haenelt reference pointed out by the referee and think it is highly relevant to our paper

Change: 1. Review image 2. Inclusion of the Haenelt-reference.

Author response image 2.

Myelin stripes of the elephant trunk module visualized by Gold-chloride staining according to Schmued. A, Low magnification micrograph of the trunk module of African elephant Indra stained with AuCl according to Schmued. The putative finger is to the left, proximal is to the right. Myelin stripes can easily be recognized. The white box indicates the area shown in B. B, high magnification micrograph of two myelin stripes. Individual gold-stained (black) axons organized in myelin stripes can be recognized.

Schmued, L. C. (1990). A rapid, sensitive histochemical stain for myelin in frozen brain sections. Journal of Histochemistry & Cytochemistry,38(5), 717-720.

Are the "bumps" in any way "analogous" to the "brain warts" seen in entorhinal areas of some human brains (G. W. van Hoesen and A. Solodkin (1993)? 

Comment: We think this is a similar phenomenon.

Change: We included the Hoesen and A. Solodkin (1993) reference in our discussion.

At least slightly more background (ie, a separate section or, if necessary, supplement) would be helpful, going into more detail on the several subdivisions of the ION and if these undergo major alterations in the elephant.

Comment: The strength of the paper is the detailed delineation of the trunk module, based on myelin stripes and isomorphism. We don’t think we have strong evidence on ION subdivisions, because it appears the trigeminal tract cannot be easily traced in elephants. Accordingly, we find it difficult to add information here.

Change: None.

Is there evidence from the literature of other conspicuous gross anatomical translocations, in any species, especially in subcortical regions? 

Comment: The best example that comes to mind is the star-nosed mole brainstem. There is a beautiful paper comparing the star-nosed mole brainstem to the normal mole brainstem (Catania et al 2011). The principal trigeminal nucleus in the star-nosed mole is far more rostral and also more medial than in the mole; still, such rearrangements are minor compared to what we propose in elephants.

Catania, Kenneth C., Duncan B. Leitch, and Danielle Gauthier. "A star in the brainstem reveals the first step of cortical magnification." PloS one 6.7 (2011): e22406.

Change: None.

(3) A major point concerns the isomorphism between the putative trigeminal nuclei and the trunk specialization. I think this can be much better presented, at least with more discussion and other examples. The Authors mention about the rodent "barrels," but it seemed strange to me that they do not refer to their own results in pig (C. Ritter et al., 2023) nor the work from Ken Catania, 2002 (star-nosed mole; "fingerprints in the brain") or other that might be appropriate. I concur with the Reviewer that there should be more comparative data. 

Comment: We agree.

Change: We added a discussion of other isomorphisms including the the star-nosed mole to our paper.

(4) Textual organization could be improved. 

The Abstract all-important Introduction is a longish, semi "run-on" paragraph. At a minimum this should be broken up. The last paragraph of the Introduction puts forth five issues, but these are only loosely followed in the Results section. I think clarity and good organization is of the upmost importance in this manuscript. I recommend that the Authors begin the Results with a section on the trunk folds (currently figure 5, and discussion), continue with the several points related to the identification of the trigeminal nuclei, and continue with a parallel description of ION with more parallel data on the putative trigeminal and IO structures (currently referee Table 1, but incorporate into the text and add higher magnification of nucleus-specific cell types in the IO and trigeminal nuclei). Relevant comparative data should be included in the Discussion.

Comment: 1. We agree with the referee that our abstract needed to be revised. 2. We also think that our ms was heavily altered by the insertion of the new Figure 2, which complemented Figure 1 from our first submission and is concerned with the identification of the inferior olive. From a standpoint of textual flow such changes were not ideal, but the revisions massively added to the certainty with which we identify the trigeminal nuclei. Thus, although we are not as content as we were with the flow, we think the ms advanced in the revision process and we would like to keep the Figure sequence as is. 3. We already noted above that we included additional comparative evidence.

Change: 1. We revised our abstract. 2. We added comparative evidence.

Reviewer #5 (Recommendations For The Authors): 

The data is invaluable and provides insights into some of the largest mammals on the planet. 

Comment: We are incredibly thankful for this positive assessment.

Reviewer #2 (Public Review):

Here I submit my previous review and a great deal of additional information following on from the initial review and the response by the authors.

* Initial Review *

Assessment:

This manuscript is based upon the unprecedented identification of an apparently highly unusual trigeminal nuclear organization within the elephant brainstem, related to a large trigeminal nerve in these animals. The apparently highly specialized elephant trigeminal nuclear complex identified in the current study has been classified as the inferior olivary nuclear complex in four previous studies of the elephant brainstem. The entire study is predicated upon the correct identification of the trigeminal sensory nuclear complex and the inferior olivary nuclear complex in the elephant, and if this is incorrect, then the remainder of the manuscript is merely unsupported speculation. There are many reasons indicating that the trigeminal nuclear complex is misidentified in the current study, rendering the entire study, and associated speculation, inadequate at best, and damaging in terms of understanding elephant brains and behaviour at worst.

Original Public Review:

The authors describe what they assert to be a very unusual trigeminal nuclear complex in the brainstem of elephants, and based on this, follow with many speculations about how the trigeminal nuclear complex, as identified by them, might be organized in terms of the sensory capacity of the elephant trunk.<br /> The identification of the trigeminal nuclear complex/inferior olivary nuclear complex in the elephant brainstem is the central pillar of this manuscript from which everything else follows, and if this is incorrect, then the entire manuscript fails, and all the associated speculations become completely unsupported.

The authors note that what they identify as the trigeminal nuclear complex has been identified as the inferior olivary nuclear complex by other authors, citing Shoshani et al. (2006; 10.1016/j.brainresbull.2006.03.016) and Maseko et al (2013; 10.1159/000352004), but fail to cite either Verhaart and Kramer (1958; PMID 13841799) or Verhaart (1962; 10.1515/9783112519882-001). These four studies are in agreement, but the current study differs.

Let's assume for the moment that the four previous studies are all incorrect and the current study is correct. This would mean that the entire architecture and organization of the elephant brainstem is significantly rearranged in comparison to ALL other mammals, including humans, previously studied (e.g. Kappers et al. 1965, The Comparative Anatomy of the Nervous System of Vertebrates, Including Man, Volume 1 pp. 668-695) and the closely related manatee (10.1002/ar.20573). This rearrangement necessitates that the trigeminal nuclei would have had to "migrate" and shorten rostrocaudally, specifically and only, from the lateral aspect of the brainstem where these nuclei extend from the pons through to the cervical spinal cord (e.g. the Paxinos and Watson rat brain atlases), the to the spatially restricted ventromedial region of specifically and only the rostral medulla oblongata. According to the current paper the inferior olivary complex of the elephant is very small and located lateral to their trigeminal nuclear complex, and the region from where the trigeminal nuclei are located by others appears to be just "lateral nuclei" with no suggestion of what might be there instead.

Such an extraordinary rearrangement of brainstem nuclei would require a major transformation in the manner in which the mutations, patterning, and expression of genes and associated molecules during development occur. Such a major change is likely to lead to lethal phenotypes, making such a transformation extremely unlikely. Variations in mammalian brainstem anatomy are most commonly associated with quantitative changes rather than qualitative changes (10.1016/B978-0-12-804042-3.00045-2).

The impetus for the identification of the unusual brainstem trigeminal nuclei in the current study rests upon a previous study from the same laboratory (10.1016/j.cub.2021.12.051) that estimated that the number of axons contained in the infraorbital branch of the trigeminal nerve that innervate the sensory surfaces of the trunk is approximately 400 000. Is this number unusual? In a much smaller mammal with a highly specialized trigeminal system, the platypus, the number of axons innervating the sensory surface of the platypus bill skin comes to 1 344 000 (10.1159/000113185). Yet, there is no complex rearrangement of the brainstem trigeminal nuclei in the brain of the developing or adult platypus (Ashwell, 2013, Neurobiology of Monotremes), despite the brainstem trigeminal nuclei being very large in the platypus (10.1159/000067195). Even in other large-brained mammals, such as large whales that do not have a trunk, the number of axons in the trigeminal nerve ranges between 400,000 and 500,000 (10.1007/978-3-319-47829-6_988-1). The lack of comparative support for the argument forwarded in the previous and current study from this laboratory, and that the comparative data indicates that the brainstem nuclei do not change in the manner suggested in the elephant, argues against the identification of the trigeminal nuclei as outlined in the current study. Moreover, the comparative studies undermine the prior claim of the authors, informing the current study, that "the elephant trigeminal ganglion ... point to a high degree of tactile specialization in elephants" (10.1016/j.cub.2021.12.051). While clearly the elephant has tactile sensitivity in the trunk, it is questionable as to whether what has been observed in elephants is indeed "truly extraordinary".

But let's look more specifically at the justification outlined in the current study to support their identification of the unusually located trigeminal sensory nuclei of the brainstem.

(1) Intense cytochrome oxidase reactivity<br /> (2) Large size of the putative trunk module<br /> (3) Elongation of the putative trunk module<br /> (4) Arrangement of these putative modules correspond to elephant head anatomy<br /> (5) Myelin stripes within the putative trunk module that apparently match trunk folds<br /> (6) Location apparently matches other mammals<br /> (7) Repetitive modular organization apparently similar to other mammals.<br /> (8) The inferior olive described by other authors lacks the lamellated appearance of this structure in other mammals

Let's examine these justifications more closely.

(1) Cytochrome oxidase histochemistry is typically used as an indicative marker of neuronal energy metabolism. The authors indicate, based on the "truly extraordinary" somatosensory capacities of the elephant trunk, that any nuclei processing this tactile information should be highly metabolically active, and thus should react intensely when stained for cytochrome oxidase. We are told in the methods section that the protocols used are described by Purkart et al (2022) and Kaufmann et al (2022). In neither of these cited papers is there any description, nor mention, of the cytochrome oxidase histochemistry methodology, thus we have no idea of how this histochemical staining was done. In order to obtain the best results for cytochrome oxidase histochemistry, the tissue is either processed very rapidly after buffer perfusion to remove blood or in recently perfusion-fixed tissue (e.g., 10.1016/0165-0270(93)90122-8). Given: (1) the presumably long post-mortem interval between death and fixation - "it often takes days to dissect elephants"; (2) subsequent fixation of the brains in 4% paraformaldehyde for "several weeks"; (3) The intense cytochrome oxidase reactivity in the inferior olivary complex of the laboratory rat (Gonzalez-Lima, 1998, Cytochrome oxidase in neuronal metabolism and Alzheimer's diseases); and (4) The lack of any comparative images from other stained portions of the elephant brainstem; it is difficult to support the justification as forwarded by the authors. It is likely that the histochemical staining observed is background reactivity from the use of diaminobenzidine in the staining protocol. Thus, this first justification is unsupported.<br /> Justifications (2), (3), and (4) are sequelae from justification (1). In this sense, they do not count as justifications, but rather unsupported extensions.

(4) and (5) These are interesting justifications, as the paper has clear internal contradictions, and (5) is a sequelae of (4). The reader is led to the concept that the myelin tracts divide the nuclei into sub-modules that match the folding of the skin on the elephant trunk. One would then readily presume that these myelin tracts are in the incoming sensory axons from the trigeminal nerve. However, the authors note that this is not the case: "Our observations on trunk module myelin stripes are at odds with this view of myelin. Specifically, myelin stripes show no tapering (which we would expect if axons divert off into the tissue). More than that, there is no correlation between myelin stripe thickness (which presumably correlates with axon numbers) and trigeminal module neuron numbers. Thus, there are numerous myelinated axons, where we observe few or no trigeminal neurons. These observations are incompatible with the idea that myelin stripes form an axonal 'supply' system or that their prime function is to connect neurons. What do myelin stripe axons do, if they do not connect neurons? We suggest that myelin stripes serve to separate rather than connect neurons." So, we are left with the observation that the myelin stripes do not pass afferent trigeminal sensory information from the "truly extraordinary" trunk skin somatic sensory system, and rather function as units that separate neurons - but to what end? It appears that the myelin stripes are more likely to be efferent axonal bundles leaving the nuclei (to form the olivocerebellar tract). This justification is unsupported.

(6) The authors indicate that the location of these nuclei matches that of the trigeminal nuclei in other mammals. This is not supported in any way. In ALL other mammals in which the trigeminal nuclei of the brainstem have been reported they are found in the lateral aspect of the brainstem, bordered laterally by the spinal trigeminal tract. This is most readily seen and accessible in the Paxinos and Watson rat brain atlases. The authors indicate that the trigeminal nuclei are medial to the facial nerve nucleus, but in every other species, the trigeminal sensory nuclei are found lateral to the facial nerve nucleus. This is most salient when examining a close relative, the manatee (10.1002/ar.20573), where the location of the inferior olive and the trigeminal nuclei matches that described by Maseko et al (2013) for the African elephant. This justification is not supported.

(7) The dual to quadruple repetition of rostro-caudal modules within the putative trigeminal nucleus as identified by the authors relies on the fact that in the neurotypical mammal, there are several trigeminal sensory nuclei arranged in a column running from the pons to the cervical spinal cord, these include (nomenclature from Paxinos and Watson in roughly rostral to caudal order) the Pr5VL, Pr5DM, Sp5O, Sp5I, and Sp5C. But, these nuclei are all located far from the midline and lateral to the facial nerve nucleus, unlike what the authors describe in the elephants. These rostrocaudal modules are expanded upon in Figure 2, and it is apparent from what is shown that the authors are attributing other brainstem nuclei to the putative trigeminal nuclei to confirm their conclusion. For example, what they identify as the inferior olive in figure 2D is likely the lateral reticular nucleus as identified by Maseko et al (2013). This justification is not supported.

(8) In primates and related species, there is a distinct banded appearance of the inferior olive, but what has been termed the inferior olive in the elephant by other authors does not have this appearance, rather, and specifically, the largest nuclear mass in the region (termed the principal nucleus of the inferior olive by Maseko et al, 2013, but Pr5, the principal trigeminal nucleus in the current paper) overshadows the partial banded appearance of the remaining nuclei in the region (but also drawn by the authors of the current paper). Thus, what is at debate here is whether the principal nucleus of the inferior olive can take on a nuclear shape rather than evince a banded appearance. The authors of this paper use this variance as justification that this cluster of nuclei could not possibly be the inferior olive. Such a "semi-nuclear/banded" arrangement of the inferior olive is seen in, for example, giraffe (10.1016/j.jchemneu.2007.05.003), domestic dog, polar bear, and most specifically the manatee (a close relative of the elephant) (brainmuseum.org; 10.1002/ar.20573). This justification is not supported.

Thus, all the justifications forwarded by the authors are unsupported. Based on methodological concerns, prior comparative mammalian neuroanatomy, and prior studies in the elephant and closely related species, the authors fail to support their notion that what was previously termed the inferior olive in the elephant is actually the trigeminal sensory nuclei. Given this failure, the justifications provided above that are sequelae also fail. In this sense, the entire manuscript and all the sequelae are not supported.

What the authors have not done is to trace the pathway of the large trigeminal nerve in the elephant brainstem, as was done by Maseko et al (2013), which clearly shows the internal pathways of this nerve, from the branch that leads to the fifth mesencephalic nucleus adjacent to the periventricular grey matter, through to the spinal trigeminal tract that extends from the pons to the spinal cord in a manner very similar to all other mammals. Nor have they shown how the supposed trigeminal information reaches the putative trigeminal nuclei in the ventromedial rostral medulla oblongata. These are but two examples of many specific lines of evidence that would be required to support their conclusions. Clearly tract tracing methods, such as cholera toxin tracing of peripheral nerves cannot be done in elephants, thus the neuroanatomy must be done properly and with attention to detail to support the major changes indicated by the authors.

So what are these "bumps" in the elephant brainstem?

Four previous authors indicate that these bumps are the inferior olivary nuclear complex. Can this be supported?

The inferior olivary nuclear complex acts "as a relay station between the spinal cord (n.b. trigeminal input does reach the spinal cord via the spinal trigeminal tract) and the cerebellum, integrating motor and sensory information to provide feedback and training to cerebellar neurons" (https://www.ncbi.nlm.nih.gov/books/NBK542242/). The inferior olivary nuclear complex is located dorsal and medial to the pyramidal tracts (which were not labelled in the current study by the authors but are clearly present in Fig. 1C and 2A) in the ventromedial aspect of the rostral medulla oblongata. This is precisely where previous authors have identified the inferior olivary nuclear complex and what the current authors assign to their putative trigeminal nuclei. The neurons of the inferior olivary nuclei project, via the olivocerebellar tract to the cerebellum to terminate in the climbing fibres of the cerebellar cortex.

Elephants have the largest (relative and absolute) cerebellum of all mammals (10.1002/ar.22425), this cerebellum contains 257 x109 neurons (10.3389/fnana.2014.00046; three times more than the entire human brain, 10.3389/neuro.09.031.2009). Each of these neurons appears to be more structurally complex than the homologous neurons in other mammals (10.1159/000345565; 10.1007/s00429-010-0288-3). In the African elephant, the neurons of the inferior olivary nuclear complex are described by Maseko et al (2013) as being both calbindin and calretinin immunoreactive. Climbing fibres in the cerebellar cortex of the African elephant are clearly calretinin immunopositive and also are likely to contain calbindin (10.1159/000345565). Given this, would it be surprising that the inferior olivary nuclear complex of the elephant is enlarged enough to create a very distinct bump in exactly the same place where these nuclei are identified in other mammals?

What about the myelin stripes? These are most likely to be the origin of the olivocerebellar tract and probably only have a coincidental relationship to the trunk. Thus, given what we know, the inferior olivary nuclear complex as described in other studies, and the putative trigeminal nuclear complex as described in the current study, is the elephant inferior olivary nuclear complex. It is not what the authors believe it to be, and they do not provide any evidence that discounts the previous studies. The authors are quite simply put, wrong. All the speculations that flow from this major neuroanatomical error are therefore science fiction rather than useful additions to the scientific literature.

What do the authors actually have?<br /> The authors have interesting data, based on their Golgi staining and analysis, of the inferior olivary nuclear complex in the elephant.

* Review of Revised Manuscript *

Assessment:

There is a clear dichotomy between the authors and this reviewer regarding the identification of specific structures, namely the inferior olivary nuclear complex and the trigeminal nuclear complex, in the brainstem of the elephant. The authors maintain the position that in the elephant alone, irrespective of all the published data on other mammals and previously published data on the elephant brainstem, these two nuclear complexes are switched in location. The authors maintain that their interpretation is correct, but this reviewer maintains that this interpretation is erroneous. The authors expressed concern that the remainder of the paper was not addressed by the reviewer, but the reviewer maintains that these sequelae to the misidentification of nuclear complexes in the elephant brainstem render any of these speculations irrelevant as the critical structures are incorrectly identified. It is this reviewer's opinion that this paper is incorrect. I provide a lot of detail below in order to provide support to the opinion I express.

Public Review of Current Submission:

As indicated in my previous review of this manuscript (see above), it is my opinion that the authors have misidentified, and indeed switched, the inferior olivary nuclear complex (IO) and the trigeminal nuclear complex (Vsens). It is this specific point only that I will address in this second review, as this is the crucial aspect of this paper - if the identification of these nuclear complexes in the elephant brainstem by the authors is incorrect, the remainder of the paper does not have any scientific validity.

The authors, in their response to my initial review, claim that I "bend" the comparative evidence against them. They further claim that as all other mammalian species exhibit a "serrated" appearance of the inferior olive, and as the elephant does not exhibit this appearance, what was previously identified as the inferior olive is actually the trigeminal nucleus and vice versa.

For convenience, I will refer to IOM and VsensM as the identification of these structures according to Maseko et al (2013) and other authors and will use IOR and VsensR to refer to the identification forwarded in the study under review.<br /> The IOM/VsensR certainly does not have a serrated appearance in elephants. Indeed, from the plates supplied by the authors in response (Referee Fig. 2), the cytochrome oxidase image supplied and the image from Maseko et al (2013) shows a very similar appearance. There is no doubt that the authors are identifying structures that closely correspond to those provided by Maseko et al (2013). It is solely a contrast in what these nuclear complexes are called and the functional sequelae of the identification of these complexes (are they related to the trunk sensation or movement controlled by the cerebellum?) that is under debate.

Elephants are part of the Afrotheria, thus the most relevant comparative data to resolve this issue will be the identification of these nuclei in other Afrotherian species. Below I provide images of these nuclear complexes, labelled in the standard nomenclature, across several Afrotherian species.

(A) Lesser hedgehog tenrec (Echinops telfairi)

Tenrecs brains are the most intensively studied of the Afrotherian brains, these extensive neuroanatomical studies were undertaken primarily by Heinz Künzle. Below I append images (coronal sections stained with cresol violet) of the IO and Vsens (labelled in the standard mammalian manner) in the lesser hedgehog tenrec. It should be clear that the inferior olive is located in the ventral midline of the rostral medulla oblongata (just like the rat) and that this nucleus is not distinctly serrated. The Vsens is located in the lateral aspect of the medulla skirted laterally by the spinal trigeminal tract (Sp5). These images and the labels indicating structures correlate precisely with that provided by Künzle (1997, 10.1016/S0168- 0102(97)00034-5), see his Figure 1K,L. Thus, in the first case of a related species, there is no serrated appearance of the inferior olive, the location of the inferior olive is confirmed through connectivity with the superior colliculus (a standard connection in mammals) by Künzle (1997), and the location of Vsens is what is considered to be typical for mammals. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report.

Review image 1.

(B) Giant otter shrew (Potomogale velox)

The otter shrews are close relatives of the Tenrecs. Below I append images of cresyl violet (left column) and myelin (right column) stained coronal sections through the brainstem with the IO, Vsens and Sp5 labelled as per standard mammalian anatomy. Here we see hints of the serration of the IO as defined by the authors, but we also see many myelin stripes across the IO. Vsens is located laterally and skirted by the Sp5. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report.

Review image 2.

(C) Four-toed sengi (Petrodromus tetradactylus)

The sengis are close relatives of the Tenrecs and otter shrews, these three groups being part of the Afroinsectiphilia, a distinct branch of the Afrotheria. Below I append images of cresyl violet (left column) and myelin (right column) stained coronal sections through the brainstem with the IO, Vsens and Sp5 labelled as per standard mammalian anatomy. Here we see vague hints of the serration of the IO (as defined by the authors), and we also see many myelin stripes across the IO. Vsens is located laterally and skirted by the Sp5. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report.

Review image 3.

(D) Rock hyrax (Procavia capensis)

The hyraxes, along with the sirens and elephants form the Paenungulata branch of the Afrotheria. Below I append images of cresyl violet (left column) and myelin (right column) stained coronal sections through the brainstem with the IO, Vsens and Sp5 labelled as per the standard mammalian anatomy. Here we see hints of the serration of the IO (as defined by the authors), but we also see evidence of a more "bulbous" appearance of subnuclei of the IO (particularly the principal nucleus), and we also see many myelin stripes across the IO. Vsens is located laterally and skirted by the Sp5. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report.

Review image 4.

(E) West Indian manatee (Trichechus manatus)

The sirens are the closest extant relatives of the elephants in the Afrotheria. Below I append images of cresyl violet (top) and myelin (bottom) stained coronal sections (taken from the University of Wisconsin-Madison Brain Collection, https://brainmuseum.org, and while quite low in magnification they do reveal the structures under debate) through the brainstem with the IO, Vsens and Sp5 labelled as per standard mammalian anatomy. Here we see the serration of the IO (as defined by the authors). Vsens is located laterally and skirted by the Sp5. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report.

Review image 5.

These comparisons and the structural identification, with which the authors agree as they only distinguish the elephants from the other Afrotheria, demonstrate that the appearance of the IO can be quite variable across mammalian species, including those with a close phylogenetic affinity to the elephants. Not all mammal species possess a "serrated" appearance of the IO. Thus, it is more than just theoretically possible that the IO of the elephant appears as described prior to this study.

So what about elephants? Below I append a series of images from coronal sections through the African elephant brainstem stained for Nissl, myelin, and immunostained for calretinin. These sections are labelled according to standard mammalian nomenclature. In these complete sections of the elephant brainstem, we do not see a serrated appearance of the IOM (as described previously and in the current study by the authors). Rather the principal nucleus of the IOM appears to be bulbous in nature. In the current study, no image of myelin staining in the IOM/VsensR is provided by the authors. However, in the images I provide, we do see the reported myelin stripes in all stains - agreement between the authors and reviewer on this point. The higher magnification image to the bottom left of the plate shows one of the IOM/VsensR myelin stripes immunostained for calretinin, and within the myelin stripes axons immunopositive for calretinin are seen (labelled with an arrow). The climbing fibres of the elephant cerebellar cortex are similarly calretinin immunopositive (10.1159/000345565). In contrast, although not shown at high magnification, the fibres forming the Sp5 in the elephant (in the Maseko description, unnamed in the description of the authors) show no immunoreactivity to calretinin.

Review image 6.

Peripherin Immunostaining

In their revised manuscript the authors present immunostaining of peripherin in the elephant brainstem. This is an important addition (although it does replace the only staining of myelin provided by the authors which is unusual as the word myelin is in the title of the paper) as peripherin is known to specifically label peripheral nerves. In addition, as pointed out by the authors, peripherin also immunostains climbing fibres (Errante et al., 1998). The understanding of this staining is important in determining the identification of the IO and Vsens in the elephant, although it is not ideal for this task as there is some ambiguity. Errante and colleagues (1998; Fig. 1) show that climbing fibres are peripherin-immunopositive in the rat. But what the authors do not evaluate is the extensive peripherin staining in the rat Sp5 in the same paper (Errante et al, 1998, Fig. 2). The image provided by the authors of their peripherin immunostaining (their new Figure 2) shows what I would call the Sp5 of the elephant to be strongly peripherin immunoreactive, just like the rat shown in Errant et al (1998), and moreover in the precise position of the rat Sp5! This makes sense as this is where the axons subserving the "extraordinary" tactile sensitivity of the elephant trunk would be found (in the standard model of mammalian brainstem anatomy). Interestingly, the peripherin immunostaining in the elephant is clearly lamellated...this coincides precisely with the description of the trigeminal sensory nuclei in the elephant by Maskeo et al (2013) as pointed out by the authors in their rebuttal. Errante et al (1998) also point out peripherin immunostaining in the inferior olive, but according to the authors this is only "weakly present" in the elephant IOM/VsensR. This latter point is crucial. Surely if the elephant has an extraordinary sensory innervation from the trunk, with 400,000 axons entering the brain, the VsensR/IOM should be highly peripherin-immunopositive, including the myelinated axon bundles?! In this sense, the authors argue against their own interpretation - either the elephant trunk is not a highly sensitive tactile organ, or the VsensR is not the trigeminal nuclei it is supposed to be.

Summary:

(1) Comparative data of species closely related to elephants (Afrotherians) demonstrates that not all mammals exhibit the "serrated" appearance of the principal nucleus of the inferior olive.

(2) The location of the IO and Vsens as reported in the current study (IOR and VsensR) would require a significant, and unprecedented, rearrangement of the brainstem in the elephants independently. I argue that the underlying molecular and genetic changes required to achieve this would be so extreme that it would lead to lethal phenotypes. Arguing that the "switcheroo" of the IO and Vsens does occur in the elephant (and no other mammals) and thus doesn't lead to lethal phenotypes is a circular argument that cannot be substantiated.

(3) Myelin stripes in the subnuclei of the inferior olivary nuclear complex are seen across all related mammals as shown above. Thus, the observation made in the elephant by the authors in what they call the VsensR, is similar to that seen in the IO of related mammals, especially when the IO takes on a more bulbous appearance. These myelin stripes are the origin of the olivocerebellar pathway and are indeed calretinin immunopositive in the elephant as I show.

(4) What the authors see aligns perfectly with what has been described previously, the only difference being the names that nuclear complexes are being called. But identifying these nuclei is important, as any functional sequelae, as extensively discussed by the authors, is entirely dependent upon accurately identifying these nuclei.

(4) The peripherin immunostaining scores an own goal - if peripherin is marking peripheral nerves (as the authors and I believe it is), then why is the VsensR/IOM only "weakly positive" for this stain? This either means that the "extraordinary" tactile sensitivity of the elephant trunk is non-existent, or that the authors have misinterpreted this staining. That there is extensive staining in the fibre pathway dorsal and lateral to the IOR (which I call the spinal trigeminal tract), supports the idea that the authors have misinterpreted their peripherin immunostaining.

(5) Evolutionary expediency. The authors argue that what they report is an expedient way in which to modify the organisation of the brainstem in the elephant to accommodate the "extraordinary" tactile sensitivity. I disagree. As pointed out in my first review, the elephant cerebellum is very large and comprised of huge numbers of morphologically complex neurons. The inferior olivary nuclei in all mammals studied in detail to date, give rise to the climbing fibres that terminate on the Purkinje cells of the cerebellar cortex. It is more parsimonious to argue that, in alignment with the expansion of the elephant cerebellum (for motor control of the trunk), the inferior olivary nuclei (specifically the principal nucleus) have had additional neurons added to accommodate this cerebellar expansion. Such an addition of neurons to the principal nucleus of the inferior olive could readily lead to the loss of the serrated appearance of the principal nucleus of the inferior olive and would require far less modifications in the developmental genetic program that forms these nuclei. This type of quantitative change appears to be the primary way in which structures are altered in the mammalian brainstem.

Reviewer #2 (Public Review):

Here I submit my previous review and a great deal of additional information following on from the initial review and the response by the authors.

* Initial Review *

Assessment:

This manuscript is based upon the unprecedented identification of an apparently highly unusual trigeminal nuclear organization within the elephant brainstem, related to a large trigeminal nerve in these animals. The apparently highly specialized elephant trigeminal nuclear complex identified in the current study has been classified as the inferior olivary nuclear complex in four previous studies of the elephant brainstem. The entire study is predicated upon the correct identification of the trigeminal sensory nuclear complex and the inferior olivary nuclear complex in the elephant, and if this is incorrect, then the remainder of the manuscript is merely unsupported speculation. There are many reasons indicating that the trigeminal nuclear complex is misidentified in the current study, rendering the entire study, and associated speculation, inadequate at best, and damaging in terms of understanding elephant brains and behaviour at worst.

Original Public Review:

The authors describe what they assert to be a very unusual trigeminal nuclear complex in the brainstem of elephants, and based on this, follow with many speculations about how the trigeminal nuclear complex, as identified by them, might be organized in terms of the sensory capacity of the elephant trunk.<br /> The identification of the trigeminal nuclear complex/inferior olivary nuclear complex in the elephant brainstem is the central pillar of this manuscript from which everything else follows, and if this is incorrect, then the entire manuscript fails, and all the associated speculations become completely unsupported.

The authors note that what they identify as the trigeminal nuclear complex has been identified as the inferior olivary nuclear complex by other authors, citing Shoshani et al. (2006; 10.1016/j.brainresbull.2006.03.016) and Maseko et al (2013; 10.1159/000352004), but fail to cite either Verhaart and Kramer (1958; PMID 13841799) or Verhaart (1962; 10.1515/9783112519882-001). These four studies are in agreement, the current study differs.

Let's assume for the moment that the four previous studies are all incorrect and the current study is correct. This would mean that the entire architecture and organization of the elephant brainstem is significantly rearranged in comparison to ALL other mammals, including humans, previously studied (e.g. Kappers et al. 1965, The Comparative Anatomy of the Nervous System of Vertebrates, Including Man, Volume 1 pp. 668-695) and the closely related manatee (10.1002/ar.20573). This rearrangement necessitates that the trigeminal nuclei would have had to "migrate" and shorten rostrocaudally, specifically and only, from the lateral aspect of the brainstem where these nuclei extend from the pons through to the cervical spinal cord (e.g. the Paxinos and Watson rat brain atlases), the to the spatially restricted ventromedial region of specifically and only the rostral medulla oblongata. According to the current paper the inferior olivary complex of the elephant is very small and located lateral to their trigeminal nuclear complex, and the region from where the trigeminal nuclei are located by others, appears to be just "lateral nuclei" with no suggestion of what might be there instead.

Such an extraordinary rearrangement of brainstem nuclei would require a major transformation in the manner in which the mutations, patterning, and expression of genes and associated molecules during development occurs. Such a major change is likely to lead to lethal phenotypes, making such a transformation extremely unlikely. Variations in mammalian brainstem anatomy are most commonly associated with quantitative changes rather than qualitative changes (10.1016/B978-0-12-804042-3.00045-2).

The impetus for the identification of the unusual brainstem trigeminal nuclei in the current study rests upon a previous study from the same laboratory (10.1016/j.cub.2021.12.051) that estimated that the number of axons contained in the infraorbital branch of the trigeminal nerve that innervate the sensory surfaces of the trunk is approximately 400 000. Is this number unusual? In a much smaller mammal with a highly specialized trigeminal system, the platypus, the number of axons innervating the sensory surface of the platypus bill skin comes to 1 344 000 (10.1159/000113185). Yet, there is no complex rearrangement of the brainstem trigeminal nuclei in the brain of the developing or adult platypus (Ashwell, 2013, Neurobiology of Monotremes), despite the brainstem trigeminal nuclei being very large in the platypus (10.1159/000067195). Even in other large-brained mammals, such as large whales that do not have a trunk, the number of axons in the trigeminal nerve ranges between 400 000 and 500 000 (10.1007/978-3-319-47829-6_988-1). The lack of comparative support for the argument forwarded in the previous and current study from this laboratory, and that the comparative data indicates that the brainstem nuclei do not change in the manner suggested in the elephant, argues against the identification of the trigeminal nuclei as outlined in the current study. Moreover, the comparative studies undermine the prior claim of the authors, informing the current study, that "the elephant trigeminal ganglion ... point to a high degree of tactile specialization in elephants" (10.1016/j.cub.2021.12.051). While clearly the elephant has tactile sensitivity in the trunk, it is questionable as to whether what has been observed in elephants is indeed "truly extraordinary".

But let's look more specifically at the justification outlined in the current study to support their identification of the unusual located trigeminal sensory nuclei of the brainstem.

(1) Intense cytochrome oxidase reactivity<br /> (2) Large size of the putative trunk module<br /> (3) Elongation of the putative trunk module<br /> (4) Arrangement of these putative modules correspond to elephant head anatomy<br /> (5) Myelin stripes within the putative trunk module that apparently match trunk folds<br /> (6) Location apparently matches other mammals<br /> (7) Repetitive modular organization apparently similar to other mammals.<br /> (8) The inferior olive described by other authors lacks the lamellated appearance of this structure in other mammals

Let's examine these justifications more closely.

(1) Cytochrome oxidase histochemistry is typically used as an indicative marker of neuronal energy metabolism. The authors indicate, based on the "truly extraordinary" somatosensory capacities of the elephant trunk, that any nuclei processing this tactile information should be highly metabolically active, and thus should react intensely when stained for cytochrome oxidase. We are told in the methods section that the protocols used are described by Purkart et al (2022) and Kaufmann et al (2022). In neither of these cited papers is there any description, nor mention, of the cytochrome oxidase histochemistry methodology, thus we have no idea of how this histochemical staining was done. In order to obtain the best results for cytochrome oxidase histochemistry, the tissue is either processed very rapidly after buffer perfusion to remove blood or in recently perfusion-fixed tissue (e.g., 10.1016/0165-0270(93)90122-8). Given: (1) the presumably long post-mortem interval between death and fixation - "it often takes days to dissect elephants"; (2) subsequent fixation of the brains in 4% paraformaldehyde for "several weeks"; (3) The intense cytochrome oxidase reactivity in the inferior olivary complex of the laboratory rat (Gonzalez-Lima, 1998, Cytochrome oxidase in neuronal metabolism and Alzheimer's diseases); and (4) The lack of any comparative images from other stained portions of the elephant brainstem; it is difficult to support the justification as forwarded by the authors. It is likely that the histochemical staining observed is background reactivity from the use of diaminobenzidine in the staining protocol. Thus, this first justification is unsupported.<br /> Justifications (2), (3), and (4) are sequelae from justification (1). In this sense, they do not count as justifications, but rather unsupported extensions.

(4) and (5) These are interesting justifications, as the paper has clear internal contradictions, and (5) is a sequelae of (4). The reader is led to the concept that the myelin tracts divide the nuclei into sub-modules that match the folding of the skin on the elephant trunk. One would then readily presume that these myelin tracts are in the incoming sensory axons from the trigeminal nerve. However, the authors note that this is not the case: "Our observations on trunk module myelin stripes are at odds with this view of myelin. Specifically, myelin stripes show no tapering (which we would expect if axons divert off into the tissue). More than that, there is no correlation between myelin stripe thickness (which presumably correlates with axon numbers) and trigeminal module neuron numbers. Thus, there are numerous myelinated axons, where we observe few or no trigeminal neurons. These observations are incompatible with the idea that myelin stripes form an axonal 'supply' system or that their prime function is to connect neurons. What do myelin stripe axons do, if they do not connect neurons? We suggest that myelin stripes serve to separate rather than connect neurons." So, we are left with the observation that the myelin stripes do not pass afferent trigeminal sensory information from the "truly extraordinary" trunk skin somatic sensory system, and rather function as units that separate neurons - but to what end? It appears that the myelin stripes are more likely to be efferent axonal bundles leaving the nuclei (to form the olivocerebellar tract). This justification is unsupported.

(6) The authors indicate that the location of these nuclei matches that of the trigeminal nuclei in other mammals. This is not supported in any way. In ALL other mammals in which the trigeminal nuclei of the brainstem have been reported they are found in the lateral aspect of the brainstem, bordered laterally by the spinal trigeminal tract. This is most readily seen and accessible in the Paxinos and Watson rat brain atlases. The authors indicate that the trigeminal nuclei are medial to the facial nerve nucleus, but in every other species the trigeminal sensory nuclei are found lateral to the facial nerve nucleus. This is most salient when examining a close relative, the manatee (10.1002/ar.20573), where the location of the inferior olive and the trigeminal nuclei matches that described by Maseko et al (2013) for the African elephant. This justification is not supported.

(7) The dual to quadruple repetition of rostro-caudal modules within the putative trigeminal nucleus as identified by the authors relies on the fact that in the neurotypical mammal, there are several trigeminal sensory nuclei arranged in a column running from the pons to the cervical spinal cord, these include (nomenclature from Paxinos and Watson in roughly rostral to caudal order) the Pr5VL, Pr5DM, Sp5O, Sp5I, and Sp5C. But, these nuclei are all located far from the midline and lateral to the facial nerve nucleus, unlike what the authors describe in the elephants. These rostrocaudal modules are expanded upon in Figure 2, and it is apparent from what is shown is that the authors are attributing other brainstem nuclei to the putative trigeminal nuclei to confirm their conclusion. For example, what they identify as the inferior olive in figure 2D is likely the lateral reticular nucleus as identified by Maseko et al (2013). This justification is not supported.

(8) In primates and related species, there is a distinct banded appearance of the inferior olive, but what has been termed the inferior olive in the elephant by other authors does not have this appearance, rather, and specifically, the largest nuclear mass in the region (termed the principal nucleus of the inferior olive by Maseko et al, 2013, but Pr5, the principal trigeminal nucleus in the current paper) overshadows the partial banded appearance of the remaining nuclei in the region (but also drawn by the authors of the current paper). Thus, what is at debate here is whether the principal nucleus of the inferior olive can take on a nuclear shape rather than evince a banded appearance. The authors of this paper use this variance as justification that this cluster of nuclei could not possibly be the inferior olive. Such a "semi-nuclear/banded" arrangement of the inferior olive is seen in, for example, giraffe (10.1016/j.jchemneu.2007.05.003), domestic dog, polar bear, and most specifically the manatee (a close relative of the elephant) (brainmuseum.org; 10.1002/ar.20573). This justification is not supported.

Thus, all the justifications forwarded by the authors are unsupported. Based on methodological concerns, prior comparative mammalian neuroanatomy, and prior studies in the elephant and closely related species, the authors fail to support their notion that what was previously termed the inferior olive in the elephant is actually the trigeminal sensory nuclei. Given this failure, the justifications provided above that are sequelae also fail. In this sense, the entire manuscript and all the sequelae are not supported.

What the authors have not done is to trace the pathway of the large trigeminal nerve in the elephant brainstem, as was done by Maseko et al (2013), which clearly shows the internal pathways of this nerve, from the branch that leads to the fifth mesencephalic nucleus adjacent to the periventricular grey matter, through to the spinal trigeminal tract that extends from the pons to the spinal cord in a manner very similar to all other mammals. Nor have they shown how the supposed trigeminal information reaches the putative trigeminal nuclei in the ventromedial rostral medulla oblongata. These are but two examples of many specific lines of evidence that would be required to support their conclusions. Clearly tract tracing methods, such as cholera toxin tracing of peripheral nerves cannot be done in elephants, thus the neuroanatomy must be done properly and with attention to details to support the major changes indicated by the authors.

So what are these "bumps" in the elephant brainstem?

Four previous authors indicate that these bumps are the inferior olivary nuclear complex. Can this be supported?

The inferior olivary nuclear complex acts "as a relay station between the spinal cord (n.b. trigeminal input does reach the spinal cord via the spinal trigeminal tract) and the cerebellum, integrating motor and sensory information to provide feedback and training to cerebellar neurons" (https://www.ncbi.nlm.nih.gov/books/NBK542242/). The inferior olivary nuclear complex is located dorsal and medial to the pyramidal tracts (which were not labelled in the current study by the authors but are clearly present in Fig. 1C and 2A) in the ventromedial aspect of the rostral medulla oblongata. This is precisely where previous authors have identified the inferior olivary nuclear complex and what the current authors assign to their putative trigeminal nuclei. The neurons of the inferior olivary nuclei project, via the olivocerebellar tract to the cerebellum to terminate in the climbing fibres of the cerebellar cortex.

Elephants have the largest (relative and absolute) cerebellum of all mammals (10.1002/ar.22425), this cerebellum contains 257 x109 neurons (10.3389/fnana.2014.00046; three times more than the entire human brain, 10.3389/neuro.09.031.2009). Each of these neurons appears to be more structurally complex than the homologous neurons in other mammals (10.1159/000345565; 10.1007/s00429-010-0288-3). In the African elephant, the neurons of the inferior olivary nuclear complex are described by Maseko et al (2013) as being both calbindin and calretinin immunoreactive. Climbing fibres in the cerebellar cortex of the African elephant are clearly calretinin immunopositive and also are likely to contain calbindin (10.1159/000345565). Given this, would it be surprising that the inferior olivary nuclear complex of the elephant is enlarged enough to create a very distinct bump in exactly the same place where these nuclei are identified in other mammals?

What about the myelin stripes? These are most likely to be the origin of the olivocerebellar tract and probably only have a coincidental relationship to the trunk. Thus, given what we know, the inferior olivary nuclear complex as described in other studies, and the putative trigeminal nuclear complex as described in the current study, is the elephant inferior olivary nuclear complex. It is not what the authors believe it to be, and they do not provide any evidence that discounts the previous studies. The authors are quite simply put, wrong. All the speculations that flow from this major neuroanatomical error are therefore science fiction rather than useful additions to the scientific literature.

What do the authors actually have?<br /> The authors have interesting data, based on their Golgi staining and analysis, of the inferior olivary nuclear complex in the elephant.

* Review of Revised Manuscript *

Assessment:

There is a clear dichotomy between the authors and this reviewer regarding the identification of specific structures, namely the inferior olivary nuclear complex and the trigeminal nuclear complex, in the brainstem of the elephant. The authors maintain the position that in the elephant alone, irrespective of all the published data on other mammals and previously published data on the elephant brainstem, these two nuclear complexes are switched in location. The authors maintain that their interpretation is correct, this reviewer maintains that this interpretation is erroneous. The authors expressed concern that the remainder of the paper was not addressed by the reviewer, but the reviewer maintains that these sequelae to the misidentification of nuclear complexes in the elephant brainstem renders any of these speculations irrelevant as the critical structures are incorrectly identified. It is this reviewer's opinion that this paper is incorrect. I provide a lot of detail below in order to provide support to the opinion I express.

Public Review of Current Submission:

As indicated in my previous review of this manuscript (see above), it is my opinion that the authors have misidentified, and indeed switched, the inferior olivary nuclear complex (IO) and the trigeminal nuclear complex (Vsens). It is this specific point only that I will address in this second review, as this is the crucial aspect of this paper - if the identification of these nuclear complexes in the elephant brainstem by the authors is incorrect, the remainder of the paper does not have any scientific validity.

The authors, in their response to my initial review, claim that I "bend" the comparative evidence against them. They further claim that as all other mammalian species exhibit a "serrated" appearance of the inferior olive, and as the elephant does not exhibit this appearance, that what was previously identified as the inferior olive is actually the trigeminal nucleus and vice versa.

For convenience, I will refer to IOM and VsensM as the identification of these structures according to Maseko et al (2013) and other authors and will use IOR and VsensR to refer to the identification forwarded in the study under review.<br /> The IOM/VsensR certainly does not have a serrated appearance in elephants. Indeed, from the plates supplied by the authors in response (Referee Fig. 2), the cytochrome oxidase image supplied and the image from Maseko et al (2013) shows a very similar appearance. There is no doubt that the authors are identifying structures that closely correspond to those provided by Maseko et al (2013). It is solely a contrast in what these nuclear complexes are called and the functional sequelae of the identification of these complexes (are they related to the trunk sensation or movement controlled by the cerebellum?) that is under debate.

Elephants are part of the Afrotheria, thus the most relevant comparative data to resolve this issue will be the identification of these nuclei in other Afrotherian species. Below I provide images of these nuclear complexes, labelled in the standard nomenclature, across several Afrotherian species.

(A) Lesser hedgehog tenrec (Echinops telfairi)

Tenrecs brains are the most intensively studied of the Afrotherian brains, these extensive neuroanatomical studies undertaken primarily by Heinz Künzle. Below I append images (coronal sections stained with cresol violet) of the IO and Vsens (labelled in the standard mammalian manner) in the lesser hedgehog tenrec. It should be clear that the inferior olive is located in the ventral midline of the rostral medulla oblongata (just like the rat) and that this nucleus is not distinctly serrated. The Vsens is located in the lateral aspect of the medulla skirted laterally by the spinal trigeminal tract (Sp5). These images and the labels indicating structures correlate precisely with that provide by Künzle (1997, 10.1016/S0168- 0102(97)00034-5), see his Figure 1K,L. Thus, in the first case of a related species, there is no serrated appearance of the inferior olive, the location of the inferior olive is confirmed through connectivity with the superior colliculus (a standard connection in mammals) by Künzle (1997), and the location of Vsens is what is considered to be typical for mammals. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report.

Review image 1.

(B) Giant otter shrew (Potomogale velox)

The otter shrews are close relatives of the Tenrecs. Below I append images of cresyl violet (left column) and myelin (right column) stained coronal sections through the brainstem with the IO, Vsens and Sp5 labelled as per standard mammalian anatomy. Here we see hints of the serration of the IO as defined by the authors, but we also see many myelin stripes across the IO. Vsens is located laterally and skirted by the Sp5. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report.

Review image 2.

(C) Four-toed sengi (Petrodromus tetradactylus)

The sengis are close relatives of the Tenrecs and otter shrews, these three groups being part of the Afroinsectiphilia, a distinct branch of the Afrotheria. Below I append images of cresyl violet (left column) and myelin (right column) stained coronal sections through the brainstem with the IO, Vsens and Sp5 labelled as per standard mammalian anatomy. Here we see vague hints of the serration of the IO (as defined by the authors), and we also see many myelin stripes across the IO. Vsens is located laterally and skirted by the Sp5. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report.

Review image 3.

(D) Rock hyrax (Procavia capensis)

The hyraxes, along with the sirens and elephants form the Paenungulata branch of the Afrotheria. Below I append images of cresyl violet (left column) and myelin (right column) stained coronal sections through the brainstem with the IO, Vsens and Sp5 labelled as per the standard mammalian anatomy. Here we see hints of the serration of the IO (as defined by the authors), but we also see evidence of a more "bulbous" appearance of subnuclei of the IO (particularly the principal nucleus), and we also see many myelin stripes across the IO. Vsens is located laterally and skirted by the Sp5. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report.

Review image 4.

(E) West Indian manatee (Trichechus manatus)

The sirens are the closest extant relatives of the elephants in the Afrotheria. Below I append images of cresyl violet (top) and myelin (bottom) stained coronal sections (taken from the University of Wisconsin-Madison Brain Collection, https://brainmuseum.org, and while quite low in magnification they do reveal the structures under debate) through the brainstem with the IO, Vsens and Sp5 labelled as per standard mammalian anatomy. Here we see the serration of the IO (as defined by the authors). Vsens is located laterally and skirted by the Sp5. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report.

Review image 5.

These comparisons and the structural identification, with which the authors agree as they only distinguish the elephants from the other Afrotheria, demonstrate that the appearance of the IO can be quite variable across mammalian species, including those with a close phylogenetic affinity to the elephants. Not all mammal species possess a "serrated" appearance of the IO. Thus, it is more than just theoretically possible that the IO of the elephant appears as described prior to this study.

So what about elephants? Below I append a series of images from coronal sections through the African elephant brainstem stained for Nissl, myelin, and immunostained for calretinin. These sections are labelled according to standard mammalian nomenclature. In these complete sections of the elephant brainstem, we do not see a serrated appearance of the IOM (as described previously and in the current study by the authors). Rather the principal nucleus of the IOM appears to be bulbous in nature. In the current study, no image of myelin staining in the IOM/VsensR is provided by the authors. However, in the images I provide, we do see the reported myelin stripes in all stains - agreement between the authors and reviewer on this point. The higher magnification image to the bottom left of the plate shows one of the IOM/VsensR myelin stripes immunostained for calretinin, and within the myelin stripes axons immunopositive for calretinin are seen (labelled with an arrow). The climbing fibres of the elephant cerebellar cortex are similarly calretinin immunopositive (10.1159/000345565). In contrast, although not shown at high magnification, the fibres forming the Sp5 in the elephant (in the Maseko description, unnamed in the description of the authors) show no immunoreactivity to calretinin.

Review image 6.

Peripherin Immunostaining

In their revised manuscript the authors present immunostaining of peripherin in the elephant brainstem. This is an important addition (although it does replace the only staining of myelin provided by the authors which is unusual as the word myelin is in the title of the paper) as peripherin is known to specifically label peripheral nerves. In addition, as pointed out by the authors, peripherin also immunostains climbing fibres (Errante et al., 1998). The understanding of this staining is important in determining the identification of the IO and Vsens in the elephant, although it is not ideal for this task as there is some ambiguity. Errante and colleagues (1998; Fig. 1) show that climbing fibres are peripherin-immunopositive in the rat. But what the authors do not evaluate is the extensive peripherin staining in the rat Sp5 in the same paper (Errante et al, 1998, Fig. 2). The image provided by the authors of their peripherin immunostaining (their new Figure 2) shows what I would call the Sp5 of the elephant to be strongly peripherin immunoreactive, just like the rat shown in Errant et al (1998), and more over in the precise position of the rat Sp5! This makes sense as this is where the axons subserving the "extraordinary" tactile sensitivity of the elephant trunk would be found (in the standard model of mammalian brainstem anatomy). Interestingly, the peripherin immunostaining in the elephant is clearly lamellated...this coincides precisely with the description of the trigeminal sensory nuclei in the elephant by Maskeo et al (2013) as pointed out by the authors in their rebuttal. Errante et al (1998) also point out peripherin immunostaining in the inferior olive, but according to the authors this is only "weakly present" in the elephant IOM/VsensR. This latter point is crucial. Surely if the elephant has an extraordinary sensory innervation from the trunk, with 400 000 axons entering the brain, the VsensR/IOM should be highly peripherin-immunopositive, including the myelinated axon bundles?! In this sense, the authors argue against their own interpretation - either the elephant trunk is not a highly sensitive tactile organ, or the VsensR is not the trigeminal nuclei it is supposed to be.

Summary:

(1) Comparative data of species closely related to elephants (Afrotherians) demonstrates that not all mammals exhibit the "serrated" appearance of the principal nucleus of the inferior olive.

(2) The location of the IO and Vsens as reported in the current study (IOR and VsensR) would require a significant, and unprecedented, rearrangement of the brainstem in the elephants independently. I argue that the underlying molecular and genetic changes required to achieve this would be so extreme that it would lead to lethal phenotypes. Arguing that the "switcheroo" of the IO and Vsens does occur in the elephant (and no other mammals) and thus doesn't lead to lethal phenotypes is a circular argument that cannot be substantiated.

(3) Myelin stripes in the subnuclei of the inferior olivary nuclear complex are seen across all related mammals as shown above. Thus, the observation made in the elephant by the authors in what they call the VsensR, is similar to that seen in the IO of related mammals, especially when the IO takes on a more bulbous appearance. These myelin stripes are the origin of the olivocerebellar pathway, and are indeed calretinin immunopositive in the elephant as I show.

(4) What the authors see aligns perfectly with what has been described previously, the only difference being the names that nuclear complexes are being called. But identifying these nuclei is important, as any functional sequelae, as extensively discussed by the authors, is entirely dependent upon accurately identifying these nuclei.

(4) The peripherin immunostaining scores an own goal - if peripherin is marking peripheral nerves (as the authors and I believe it is), then why is the VsensR/IOM only "weakly positive" for this stain? This either means that the "extraordinary" tactile sensitivity of the elephant trunk is non-existent, or that the authors have misinterpreted this staining. That there is extensive staining in the fibre pathway dorsal and lateral to the IOR (which I call the spinal trigeminal tract), supports the idea that the authors have misinterpreted their peripherin immunostaining.

(5) Evolutionary expediency. The authors argue that what they report is an expedient way in which to modify the organisation of the brainstem in the elephant to accommodate the "extraordinary" tactile sensitivity. I disagree. As pointed out in my first review, the elephant cerebellum is very large and comprised of huge numbers of morphologically complex neurons. The inferior olivary nuclei in all mammals studied in detail to date, give rise to the climbing fibres that terminate on the Purkinje cells of the cerebellar cortex. It is more parsimonious to argue that, in alignment with the expansion of the elephant cerebellum (for motor control of the trunk), the inferior olivary nuclei (specifically the principal nucleus) have had additional neurons added to accommodate this cerebellar expansion. Such an addition of neurons to the principal nucleus of the inferior olive could readily lead to the loss of the serrated appearance of the principal nucleus of the inferior olive, and would require far less modifications in the developmental genetic program that forms these nuclei. This type of quantitative change appears to be the primary way in which structures are altered in the mammalian brainstem.

Author response:

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

eLife Assessment

This neuroimaging and electrophysiology study in a small cohort of congenital cataract patients with sight recovery aims to characterize the effects of early visual deprivation on excitatory and inhibitory balance in visual cortex. While contrasting sight-recovery with visually intact controls suggested the existence of persistent alterations in Glx/GABA ratio and aperiodic EEG signals, it provided only incomplete evidence supporting claims about the effects of early deprivation itself. The reported data were considered valuable, given the rare study population. However, the small sample sizes, lack of a specific control cohort and multiple methodological limitations will likely restrict usefulness to scientists working in this particular subfield.

We thank the reviewing editors for their consideration and updated assessment of our manuscript after its first revision.

In order to assess the effects of early deprivation, we included an age-matched, normally sighted control group recruited from the same community, measured in the same scanner and laboratory. This study design is analogous to numerous studies in permanently congenitally blind humans, which typically recruited sighted controls, but hardly ever individuals with a different, e.g. late blindness history. In order to improve the specificity of our conclusions, we used a frontal cortex voxel in addition to a visual cortex voxel (MRS). Analogously, we separately analyzed occipital and frontal electrodes (EEG).

Moreover, we relate our findings in congenital cataract reversal individuals to findings in the literature on permanent congenital blindness. Note, there are, to the best of our knowledge, neither MRS nor resting-state EEG studies in individuals with permanent late blindness.

Our participants necessarily have nystagmus and low visual acuity due to their congenital deprivation phase, and the existence of nystagmus is a recruitment criterion to diagnose congenital cataracts.

It might be interesting for future studies to investigate individuals with transient late blindness. However, such a study would be ill-motivated had we not found differences between the most “extreme” of congenital visual deprivation conditions and normally sighted individuals (analogous to why earlier research on permanent blindness investigated permanent congenitally blind humans first, rather than permanently late blind humans, or both in the same study). Any result of these future work would need the reference to our study, and neither results in these additional groups would invalidate our findings.

Since all our congenital cataract reversal individuals by definition had visual impairments, we included an eyes closed condition, both in the MRS and EEG assessment. Any group effect during the eyes closed condition cannot be due to visual acuity deficits changing the bottom-up driven visual activation.

As we detail in response to review 3, our EEG analyses followed the standards in the field.

Public Reviews:

Reviewer #1 (Public review):

Summary

In this human neuroimaging and electrophysiology study, the authors aimed to characterise effects of a period of visual deprivation in the sensitive period on excitatory and inhibitory balance in the visual cortex. They attempted to do so by comparing neurochemistry conditions ('eyes open', 'eyes closed') and resting state, and visually evoked EEG activity between ten congenital cataract patients with recovered sight (CC), and ten age-matched control participants (SC) with normal sight.

First, they used magnetic resonance spectroscopy to measure in vivo neurochemistry from two locations, the primary location of interest in the visual cortex, and a control location in the frontal cortex. Such voxels are used to provide a control for the spatial specificity of any effects, because the single-voxel MRS method provides a single sampling location. Using MR-visible proxies of excitatory and inhibitory neurotransmission, Glx and GABA+ respectively, the authors report no group effects in GABA+ or Glx, no difference in the functional conditions 'eyes closed' and 'eyes open'. They found an effect of group in the ratio of Glx/GABA+ and no similar effect in the control voxel location. They then perform multiple exploratory correlations between MRS measures and visual acuity, and report a weak positive correlation between the 'eyes open' condition and visual acuity in CC participants.

The same participants then took part in an EEG experiment. The authors selected two electrodes placed in the visual cortex for analysis and report a group difference in an EEG index of neural activity, the aperiodic intercept, as well as the aperiodic slope, considered a proxy for cortical inhibition. Control electrodes in the frontal region did not present with the same pattern. They report an exploratory correlation between the aperiodic intercept and Glx in one out of three EEG conditions.

The authors report the difference in E/I ratio, and interpret the lower E/I ratio as representing an adaptation to visual deprivation, which would have initially caused a higher E/I ratio. Although intriguing, the strength of evidence in support of this view is not strong. Amongst the limitations are the low sample size, a critical control cohort that could provide evidence for higher E/I ratio in CC patients without recovered sight for example, and lower data quality in the control voxel. Nevertheless, the study provides a rare and valuable insight into experience-dependent plasticity in the human brain.

Strengths of study

How sensitive period experience shapes the developing brain is an enduring and important question in neuroscience. This question has been particularly difficult to investigate in humans. The authors recruited a small number of sight-recovered participants with bilateral congenital cataracts to investigate the effect of sensitive period deprivation on the balance of excitation and inhibition in the visual brain using measures of brain chemistry and brain electrophysiology. The research is novel, and the paper was interesting and well written.

Limitations

Low sample size. Ten for CC and ten for SC, and further two SC participants were rejected due to lack of frontal control voxel data. The sample size limits the statistical power of the dataset and increases the likelihood of effect inflation.

In the updated manuscript, the authors have provided justification for their sample size by pointing to prior studies and the inherent difficulties in recruiting individuals with bilateral congenital cataracts. Importantly, this highlights the value the study brings to the field while also acknowledging the need to replicate the effects in a larger cohort.

Lack of specific control cohort. The control cohort has normal vision. The control cohort is not specific enough to distinguish between people with sight loss due to different causes and patients with congenital cataracts with co-morbidities. Further data from a more specific populations, such as patients whose cataracts have not been removed, with developmental cataracts, or congenitally blind participants, would greatly improve the interpretability of the main finding. The lack of a more specific control cohort is a major caveat that limits a conclusive interpretation of the results.

In the updated version, the authors have indicated that future studies can pursue comparisons between congenital cataract participants and cohorts with later sight loss.

MRS data quality differences. Data quality in the control voxel appears worse than in the visual cortex voxel. The frontal cortex MRS spectrum shows far broader linewidth than the visual cortex (Supplementary Figures). Compared to the visual voxel, the frontal cortex voxel has less defined Glx and GABA+ peaks; lower GABA+ and Glx concentrations, lower NAA SNR values; lower NAA concentrations. If the data quality is a lot worse in the FC, then small effects may not be detectable.

In the updated version, the authors have added more information that informs the reader of the MRS quality differences between voxel locations. This increases the transparency of their reporting and enhances the assessment of the results.

Because of the direction of the difference in E/I, the authors interpret their findings as representing signatures of sight improvement after surgery without further evidence, either within the study or from the literature. However, the literature suggests that plasticity and visual deprivation drives the E/I index up rather than down. Decreasing GABA+ is thought to facilitate experience dependent remodelling. What evidence is there that cortical inhibition increases in response to a visual cortex that is over-sensitised to due congenital cataracts? Without further experimental or literature support this interpretation remains very speculative.

The updated manuscript contains key reference from non-human work to justify their interpretation.

Heterogeneity in patient group. Congenital cataract (CC) patients experienced a variety of duration of visual impairment and were of different ages. They presented with co-morbidities (absorbed lens, strabismus, nystagmus). Strabismus has been associated with abnormalities in GABAergic inhibition in the visual cortex. The possible interactions with residual vision and confounds of co-morbidities are not experimentally controlled for in the correlations, and not discussed.

The updated document has addressed this caveat.

Multiple exploratory correlations were performed to relate MRS measures to visual acuity (shown in Supplementary Materials), and only specific ones shown in the main document. The authors describe the analysis as exploratory in the 'Methods' section. Furthermore, the correlation between visual acuity and E/I metric is weak, not corrected for multiple comparisons. The results should be presented as preliminary, as no strong conclusions can be made from them. They can provide a hypothesis to test in a future study.

This has now been done throughout the document and increases the transparency of the reporting.

P.16 Given the correlation of the aperiodic intercept with age ("Age negatively correlated with the aperiodic intercept across CC and SC individuals, that is, a flattening of the intercept was observed with age"), age needs to be controlled for in the correlation between neurochemistry and the aperiodic intercept. Glx has also been shown to negatively correlates with age.

This caveat has been addressed in the revised manuscript.

Multiple exploratory correlations were performed to relate MRS to EEG measures (shown in Supplementary Materials), and only specific ones shown in the main document. Given the multiple measures from the MRS, the correlations with the EEG measures were exploratory, as stated in the text, p.16, and in Fig.4. yet the introduction said that there was a prior hypothesis "We further hypothesized that neurotransmitter changes would relate to changes in the slope and intercept of the EEG aperiodic activity in the same subjects." It would be great if the text could be revised for consistency and the analysis described as exploratory.

This has been done throughout the document and increases the transparency of the reporting.

The analysis for the EEG needs to take more advantage of the available data. As far as I understand, only two electrodes were used, yet far more were available as seen in their previous study (Ossandon et al., 2023). The spatial specificity is not established. The authors could use the frontal cortex electrode (FP1, FP2) signals as a control for spatial specificity in the group effects, or even better, all available electrodes and correct for multiple comparisons. Furthermore, they could use the aperiodic intercept vs Glx in SC to evaluate the specificity of the correlation to CC.

This caveat has been addressed. The authors have added frontal electrodes to their analysis, providing an essential regional control for the visual cortex location.

Comments on the latest version:

The authors have made reasonable adjustments to their manuscript that addressed most of my comments by adding further justification for their methodology, essential literature support, pointing out exploratory analyses, limitations and adding key control analyses. Their revised manuscript has overall improved, providing valuable information, though the evidence that supports their claims is still incomplete.

We thank the reviewer for suggesting ways to improve our manuscript and carefully reassessing our revised manuscript.

Reviewer #2 (Public review):

Summary:

The study examined 10 congenitally blind patients who recovered vision through the surgical removal of bilateral dense cataracts, measuring neural activity and neuro chemical profiles from the visual cortex. The declared aim is to test whether restoring visual function after years of complete blindness impacts excitation/inhibition balance in the visual cortex.

Strengths:

The findings are undoubtedly useful for the community, as they contribute towards characterising the many ways in which this special population differs from normally sighted individuals. The combination of MRS and EEG measures is a promising strategy to estimate a fundamental physiological parameter - the balance between excitation and inhibition in the visual cortex, which animal studies show to be heavily dependent upon early visual experience. Thus, the reported results pave the way for further studies, which may use a similar approach to evaluate more patients and control groups.

Weaknesses:

The main methodological limitation is the lack of an appropriate comparison group or condition to delineate the effect of sight recovery (as opposed to the effect of congenital blindness). Few previous studies suggested that Excitation/Inhibition ratio in the visual cortex is increased in congenitally blind patients; the present study reports that E/I ratio decreases instead. The authors claim that this implies a change of E/I ratio following sight recovery. However, supporting this claim would require showing a shift of E/I after vs. before the sight-recovery surgery, or at least it would require comparing patients who did and did not undergo the sight-recovery surgery (as common in the field).

We thank the reviewer for suggesting ways to improve our manuscript and carefully reassessing our revised manuscript.

Since we have not been able to acquire longitudinal data with the experimental design of the present study in congenital cataract reversal individuals, we compared the MRS and EEG results of congenital cataract reversal individuals  to published work in congenitally permanent blind individuals. We consider this as a resource saving approach. We think that the results of our cross-sectional study now justify the costs and enormous efforts (and time for the patients who often have to travel long distances) associated with longitudinal studies in this rare population.

There are also more technical limitations related to the correlation analyses, which are partly acknowledged in the manuscript. A bland correlation between GLX/GABA and the visual impairment is reported, but this is specific to the patients group (N=10) and would not hold across groups (the correlation is positive, predicting the lowest GLX/GABA ratio values for the sighted controls - opposite of what is found). There is also a strong correlation between GLX concentrations and the EEG power at the lowest temporal frequencies. Although this relation is intriguing, it only holds for a very specific combination of parameters (of the many tested): only with eyes open, only in the patients group.

Given the exploratory nature of the correlations, we do not base the majority of our conclusions on this analysis. There are no doubts that the reported correlations need replication; however, replication is only possible after a first report. Thus, we hope to motivate corresponding analyses in further studies.

It has to be noted that in the present study significance testing for correlations were corrected for multiple comparisons, and that some findings replicate earlier reports (e.g. effects on EEG aperiodic slope, alpha power, and correlations with chronological age).

Conclusions:

The main claim of the study is that sight recovery impacts the excitation/inhibition balance in the visual cortex, estimated with MRS or through indirect EEG indices. However, due to the weaknesses outlined above, the study cannot distinguish the effects of sight recovery from those of visual deprivation. Moreover, many aspects of the results are interesting but their validation and interpretation require additional experimental work.

We interpret the group differences between individuals tested years after congenital visual deprivation and normally sighted individuals as supportive of the E/I ratio being impacted by congenital visual deprivation. In the absence of a sensitive period for the development of an E/I ratio, individuals with a transient phase of congenital blindness might have developed a visual system indistinguishable  from normally sighted individuals. As we demonstrate, this is not so. Comparing the results of congenitally blind humans with those of congenitally permanently blind humans (from previous studies) allowed us to identify changes of E/I ratio, which add to those found for congenital blindness.  

We thank the reviewer for the helpful comments and suggestions related to the first submission and first revision of our manuscript. We are keen to translate some of them into future studies.

Reviewer #3 (Public review):

This manuscript examines the impact of congenital visual deprivation on the excitatory/inhibitory (E/I) ratio in the visual cortex using Magnetic Resonance Spectroscopy (MRS) and electroencephalography (EEG) in individuals whose sight was restored. Ten individuals with reversed congenital cataracts were compared to age-matched, normally sighted controls, assessing the cortical E/I balance and its interrelationship and to visual acuity. The study reveals that the Glx/GABA ratio in the visual cortex and the intercept and aperiodic signal are significantly altered in those with a history of early visual deprivation, suggesting persistent neurophysiological changes despite visual restoration.

First of all, I would like to disclose that I am not an expert in congenital visual deprivation, nor in MRS. My expertise is in EEG (particularly in the decomposition of periodic and aperiodic activity) and statistical methods.

Although the authors addressed some of the concerns of the previous version, major concerns and flaws remain in terms of methodological and statistical approaches along with the (over)interpretation of the results. Specific concerns include:

(1 3.1) Response to Variability in Visual Deprivation<br /> Rather than listing the advantages and disadvantages of visual deprivation, I recommend providing at least a descriptive analysis of how the duration of visual deprivation influenced the measures of interest. This would enhance the depth and relevance of the discussion.

Although Review 2 and Review 3 (see below) pointed out problems in interpreting multiple correlational analyses in small samples, we addressed this request by reporting such correlations between visual deprivation history and measured EEG/MRS outcomes.

Calculating the correlation between duration of visual deprivation and behavioral or brain measures is, in fact, a common suggestion. The existence of sensitive periods, which are typically assumed to not follow a linear gradual decline of neuroplasticity, does not necessary allow predicting a correlation with duration of blindness. Daphne Maurer has additionally worked on the concept of “sleeper effects” (Maurer et al., 2007), that is, effects on the brain and behavior by early deprivation which are observed only later in life when the function/neural circuits matures.

In accordance with this reasoning, we did not observe a significant correlation between duration of visual deprivation and any of our dependent variables.

(2 3.2) Small Sample Size<br /> The issue of small sample size remains problematic. The justification that previous studies employed similar sample sizes does not adequately address the limitation in the current study. I strongly suggest that the correlation analyses should not feature prominently in the main manuscript or the abstract, especially if the discussion does not substantially rely on these correlations. Please also revisit the recommendations made in the section on statistical concerns.

In the revised manuscript, we explicitly mention that our sample size is not atypical for the special group investigated, but that a replication of our results in larger samples would foster their impact. We only explicitly mention correlations that survived stringent testing for multiple comparisons in the main manuscript.

Given the exploratory nature of the correlations, we have not based the majority of our claims on this analysis.

(3 3.3) Statistical Concerns<br /> While I appreciate the effort of conducting an independent statistical check, it merely validates whether the reported statistical parameters, degrees of freedom (df), and p-values are consistent. However, this does not address the appropriateness of the chosen statistical methods.

We did not intend for the statcheck report to justify the methods used for statistics, which we have done in a separate section with normality and homogeneity testing (Supplementary Material S9), and references to it in the descriptions of the statistical analyses (Methods, Page 13, Lines 326-329 and Page 15, Lines 400-402).

Several points require clarification or improvement:<br /> (4) Correlation Methods: The manuscript does not specify whether the reported correlation analyses are based on Pearson or Spearman correlation.

The depicted correlations are Pearson correlations. We will add this information to the Methods.

(5) Confidence Intervals: Include confidence intervals for correlations to represent the uncertainty associated with these estimates.

We have added the confidence intervals for all measured correlations to the second revision of our manuscript.

(6) Permutation Statistics: Given the small sample size, I recommend using permutation statistics, as these are exact tests and more appropriate for small datasets.

Our study focuses on a rare population, with a sample size limited by the availability of participants. Our findings provide exploratory insights rather than make strong inferential claims. To this end, we have ensured that our analysis adheres to key statistical assumptions (Shapiro-Wilk as well as Levene’s tests, Supplementary Material S9), and reported our findings with effect sizes, appropriate caution and context.

(7) Adjusted P-Values: Ensure that reported Bonferroni corrected p-values (e.g., p > 0.999) are clearly labeled as adjusted p-values where applicable.

In the revised manuscript, we have changed Figure 4 to say ‘adjusted p,’  which we indeed reported.

(8) Figure 2C

Figure 2C still lacks crucial information that the correlation between Glx/GABA ratio and visual acuity was computed solely in the control group (as described in the rebuttal letter). Why was this analysis restricted to the control group? Please provide a rationale.

Figure 2C depicts the correlation between Glx/GABA+ ratio and visual acuity in the congenital cataract reversal group, not the control group. This is mentioned in the Figure 2 legend, as well as in the main text where the figure is referred to (Page 18, Line 475).

The correlation analyses between visual acuity and MRS/EEG measures were only performed in the congenital cataract reversal group since the sighed control group comprised of individuals with vision in the normal range; thus this analyses would not make sense. Table 1 with the individual visual acuities for all participants, including the normally sighted controls, shows the low variance in the latter group.  

For variables in which no apiori group differences in variance were predicted, we performed the correlation analyses across groups (see Supplementary Material S12, S15).

We have now highlighted these motivations more clearly in the Methods of the revised manuscript (Page 16, Lines 405-410).

(9 3.4) Interpretation of Aperiodic Signal

Relying on previous studies to interpret the aperiodic slope as a proxy for excitation/inhibition (E/I) does not make the interpretation more robust.

How to interpret aperiodic EEG activity has been subject of extensive investigation. We cite studies which provide evidence from multiple species (monkeys, humans) and measurements (EEG, MEG, ECoG), including studies which pharmacologically manipulated E/I balance.

Whether our findings are robust, in fact, requires a replication study. Importantly, we analyzed the intercept of the aperiodic activity fit as well, and discuss results related to the intercept.

Quote:

“(3.4) Interpretation of aperiodic signal:

- Several recent papers demonstrated that the aperiodic signal measured in EEG or ECoG is related to various important aspects such as age, skull thickness, electrode impedance, as well as cognition. Thus, currently, very little is known about the underlying effects which influence the aperiodic intercept and slope. The entire interpretation of the aperiodic slope as a proxy for E/I is based on a computational model and simulation (as described in the Gao et al. paper).

Apart from the modeling work from Gao et al., multiple papers which have also been cited which used ECoG, EEG and MEG and showed concomitant changes in aperiodic activity with pharmacological manipulation of the E/I ratio (Colombo et al., 2019; Molina et al., 2020; Muthukumaraswamy & Liley, 2018). Further, several prior studies have interpreted changes in the aperiodic slope as reflective of changes in the E/I ratio, including studies of developmental groups (Favaro et al., 2023; Hill et al., 2022; McSweeney et al., 2023; Schaworonkow & Voytek, 2021) as well as patient groups (Molina et al., 2020; Ostlund et al., 2021).

- The authors further wrote: We used the slope of the aperiodic (1/f) component of the EEG spectrum as an estimate of E/I ratio (Gao et al., 2017; Medel et al., 2020; Muthukumaraswamy & Liley, 2018). This is a highly speculative interpretation with very little empirical evidence. These papers were conducted with ECoG data (mostly in animals) and mostly under anesthesia. Thus, these studies only allow an indirect interpretation by what the 1/f slope in EEG measurements is actually influenced.

Note that Muthukumaraswamy et al. (2018) used different types of pharmacological manipulations and analyzed periodic and aperiodic MEG activity in humans, in addition to monkey ECoG (Muthukumaraswamy & Liley, 2018). Further, Medel et al. (now published as Medel et al., 2023) compared EEG activity in addition to ECoG data after propofol administration. The interpretation of our results are in line with a number of recent studies in developing (Hill et al., 2022; Schaworonkow & Voytek, 2021) and special populations using EEG. As mentioned above, several prior studies have used the slope of the 1/f component/aperiodic activity as an indirect measure of the E/I ratio (Favaro et al., 2023; Hill et al., 2022; McSweeney et al., 2023; Molina et al., 2020; Ostlund et al., 2021; Schaworonkow & Voytek, 2021), including studies using scalp-recorded EEG from humans.

In the introduction of the revised manuscript, we have made more explicit that this metric is indirect (Page 3, Line 91), (additionally see Discussion, Page 24, Lines 644-645, Page 25, Lines 650-657).

While a full understanding of aperiodic activity needs to be provided, some convergent ideas have emerged. We think that our results contribute to this enterprise, since our study is, to the best of our knowledge, the first which assessed MRS measured neurotransmitter levels and EEG aperiodic activity. “

(10) Additionally, the authors state:

"We cannot think of how any of the exploratory correlations between neurophysiological measures and MRS measures could be accounted for by a difference e.g. in skull thickness."

(11) This could be addressed directly by including skull thickness as a covariate or visualizing it in scatterplots, for instance, by representing skull thickness as the size of the dots.

We are not aware of any study that would justify such an analysis.

Our analyses were based on previous findings in the literature.

Since to the best of our knowledge, no evidence exists that congenital cataracts go together with changes in skull thickness, and that skull thickness might selectively modulate visual cortex Glx/GABA+ but not NAA measures, we decided against following this suggestion.

Notably, the neurotransmitter concentration reported here is after tissue segmentation of the voxel region. The tissue fraction was shown to not differ between groups in the MRS voxels (Supplementary Material S4). The EEG electrode impedance was lowered to <10 kOhm in every participant (Methods, Page 13, Line 344), and preparation was identical across groups.

(12 3.5) Problems with EEG Preprocessing and Analysis

Downsampling: The decision to downsample the data to 60 Hz "to match the stimulation rate" is problematic. This choice conflates subsequent spectral analyses due to aliasing issues, as explained by the Nyquist theorem. While the authors cite prior studies (Schwenk et al., 2020; VanRullen & MacDonald, 2012) to justify this decision, these studies focused on alpha (8-12 Hz), where aliasing is less of a concern compared of analyzing aperiodic signal. Furthermore, in contrast, the current study analyzes the frequency range from 1-20 Hz, which is too narrow for interpreting the aperiodic signal as E/I. Typically, this analysis should include higher frequencies, spanning at least 1-30 Hz or even 1-45 Hz (not 20-40 Hz).

As previously mentied in the Methods (Page 15 Line 376) and the previous response, the pop_resample function used by EEGLAB applies an anti-aliasing filter, at half the resampling frequency (as per the Nyquist theorem

https://eeglab.org/tutorials/05_Preprocess/resampling.html). The upper cut off of the low pass filter set by EEGlab prior to down sampling (30 Hz) is still far above the frequency of interest in the current study  (1-20 Hz), thus allowing us to derive valid results.

Quote:

“- The authors downsampled the data to 60Hz to "to match the stimulation rate". What is the intention of this? Because the subsequent spectral analyses are conflated by this choice (see Nyquist theorem).

This data were collected as part of a study designed to evoke alpha activity with visual white-noise, which ranged in luminance with equal power at all frequencies from 1-60 Hz, restricted by the refresh rate of the monitor on which stimuli were presented (Pant et al., 2023). This paradigm and method was developed by VanRullen and colleagues (Schwenk et al., 2020; Vanrullen & MacDonald, 2012), wherein the analysis requires the same sampling rate between the presented frequencies and the EEG data. The downsampling function used here automatically applies an anti-aliasing filter (EEGLAB 2019) .”

Moreover, the resting-state data were not resampled to 60 Hz. We have made this clearer in the Methods of the second revision (Page 15, Line 367).

Our consistent results of group differences across all three EEG conditions, thus, exclude any possibility that they were driven by aliasing artifacts.

The expected effects of this anti-aliasing filter can be seen in the attached Author response image 1, showing an example participant’s spectrum in the 1-30 Hz range (as opposed to the 1-20 Hz plotted in the manuscript), clearly showing a 30-40 dB drop at 30 Hz. Any aliasing due to, for example, remaining line noise, would additionally be visible in this figure (as well as Figure 3) as a peak.

Author response image 1.

Power spectral density of one congenital cataract-reversal (CC) participant in the visual stimulation condition across all channels. The reduced power at 30 Hz shows the effects of the anti-aliasing filter applied by EEGLAB’s pop_resample function.

As we stated in the manuscript, and in previous reviews, so far there has been no consensus on the exact range of measuring aperiodic activity. We made a principled decision based on the literature (showing a knee in aperiodic fits of this dataset at 20 Hz) (Medel et al., 2023; Ossandón et al., 2023), data quality (possible contamination by line noise at higher frequencies) and the purpose of the visual stimulation experiment (to look at the lower frequency range by stimulating up to 60 Hz, thereby limiting us to quantifying below 30 Hz), that 1-20 Hz would be the fit range in this dataset.

Quote:

“(3) What's the underlying idea of analyzing two separate aperiodic slopes (20-40Hz and 1-19Hz). This is very unusual to compute the slope between 20-40 Hz, where the SNR is rather low.

"Ossandón et al. (2023), however, observed that in addition to the flatter slope of the aperiodic power spectrum in the high frequency range (20-40 Hz), the slope of the low frequency range (1-19 Hz) was steeper in both, congenital cataract-reversal individuals, as well as in permanently congenitally blind humans."

The present manuscript computed the slope between 1-20 Hz. Ossandón et al. as well as Medel et al. (2023) found a “knee” of the 1/f distribution at 20 Hz and describe further the motivations for computing both slope ranges. For example, Ossandón et al. used a data driven approach and compared single vs. dual fits and found that the latter fitted the data better. Additionally, they found the best fit if a knee at 20 Hz was used. We would like to point out that no standard range exists for the fitting of the 1/f component across the literature and, in fact, very different ranges have been used (Gao et al., 2017; Medel et al., 2023; Muthukumaraswamy & Liley, 2018). “

(13) Baseline Removal: Subtracting the mean activity across an epoch as a baseline removal step is inappropriate for resting-state EEG data. This preprocessing step undermines the validity of the analysis. The EEG dataset has fundamental flaws, many of which were pointed out in the previous review round but remain unaddressed. In its current form, the manuscript falls short of standards for robust EEG analysis. If I were reviewing for another journal, I would recommend rejection based on these flaws.

The baseline removal step from each epoch serves to remove the DC component of the recording and detrend the data. This is a standard preprocessing step (included as an option in preprocessing pipelines recommended by the EEGLAB toolbox, FieldTrip toolbox and MNE toolbox), additionally necessary to improve the efficacy of ICA decomposition (Groppe et al., 2009).

In the previous review round, a clarification of the baseline timing was requested, which we added. Beyond this request, there was no mention of the appropriateness of the baseline removal and/or a request to provide reasons for why it might not undermine the validity of the analysis.

Quote:

“- "Subsequently, baseline removal was conducted by subtracting the mean activity across the length of an epoch from every data point." The actual baseline time segment should be specified.

The time segment was the length of the epoch, that is, 1 second for the resting state conditions and 6.25 seconds for the visual stimulation conditions. This has been explicitly stated in the revised manuscript (Page 13, Line 354).”

Prior work in the time (not frequency) domain on event-related potential (ERP) analysis has suggested that the baselining step might cause spurious effects (Delorme, 2023) (although see (Tanner et al., 2016)). We did not perform ERP analysis at any stage. One recent study suggests spurious group differences in the 1/f signal might be driven by an inappropriate dB division baselining method (Gyurkovics et al., 2021), which we did not perform.

Any effect of our baselining procedure on the FFT spectrum would be below the 1 Hz range, which we did not analyze.  

Each of the preprocessing steps in the manuscript match pipelines described and published in extensive prior work. We document how multiple aspects of our EEG results replicate prior findings (Supplementary Material S15, S18, S19), reports of other experimenters, groups and locations, validating that our results are robust.

We therefore reject the claim of methodological flaws in our EEG analyses in the strongest possible terms.

Quote:

“(3.5) Problems with EEG preprocessing and analysis:

- It seems that the authors did not identify bad channels nor address the line noise issue (even a problem if a low pass filter of below-the-line noise was applied).

As pointed out in the methods and Figure 1, we only analyzed data from two occipital channels, O1 and O2 neither of which were rejected for any participant. Channel rejection was performed for the larger dataset, published elsewhere (Ossandón et al., 2023; Pant et al., 2023). As control sites we added the frontal channels FP1 and Fp2 (see Supplementary Material S14)

Neither Ossandón et al. (2023) nor Pant et al. (2023) considered frequency ranges above 40 Hz to avoid any possible contamination with line noise. Here, we focused on activity between 0 and 20 Hz, definitely excluding line noise contaminations (Methods, Page 14, Lines 365-367). The low pass filter (FIR, 1-45 Hz) guaranteed that any spill-over effects of line noise would be restricted to frequencies just below the upper cutoff frequency.

Additionally, a prior version of the analysis used spectrum interpolation to remove line noise; the group differences remained stable (Ossandón et al., 2023). We have reported this analysis in the revised manuscript (Page 14, Lines 364-357).

Further, both groups were measured in the same lab, making line noise (~ 50 Hz) as an account for the observed group effects in the 1-20 Hz frequency range highly unlikely. Finally, any of the exploratory MRS-EEG correlations would be hard to explain if the EEG parameters would be contaminated with line noise.

- What was the percentage of segments that needed to be rejected due to the 120μV criteria? This should be reported specifically for EO & EC and controls and patients.

The mean percentage of 1 second segments rejected for each resting state condition and the percentage of 6.25 long segments rejected in each group for the visual stimulation condition have been added to the revised manuscript (Supplementary Material S10), and referred to in the Methods on Page 14, Lines 372-373).

- The authors downsampled the data to 60Hz to "to match the stimulation rate". What is the intention of this? Because the subsequent spectral analyses are conflated by this choice (see Nyquist theorem).

This data were collected as part of a study designed to evoke alpha activity with visual white-noise, which changed in luminance with equal power at all frequencies from 1-60 Hz, restricted by the refresh rate of the monitor on which stimuli were presented (Pant et al., 2023). This paradigm and method was developed by VanRullen and colleagues (Schwenk et al., 2020; VanRullen & MacDonald, 2012), wherein the analysis requires the same sampling rate between the presented frequencies and the EEG data. The downsampling function used here automatically applies an anti-aliasing filter (EEGLAB 2019) .

- "Subsequently, baseline removal was conducted by subtracting the mean activity across the length of an epoch from every data point." The actual baseline time segment should be specified.

The time segment was the length of the epoch, that is, 1 second for the resting state conditions and 6.25 seconds for the visual stimulation conditions. This has now been explicitly stated in the revised manuscript (Page 14, Lines 379-380).

- "We excluded the alpha range (8-14 Hz) for this fit to avoid biasing the results due to documented differences in alpha activity between CC and SC individuals (Bottari et al., 2016; Ossandón et al., 2023; Pant et al., 2023)." This does not really make sense, as the FOOOF algorithm first fits the 1/f slope, for which the alpha activity is not relevant.

We did not use the FOOOF algorithm/toolbox in this manuscript. As stated in the Methods, we used a 1/f fit to the 1-20 Hz spectrum in the log-log space, and subtracted this fit from the original spectrum to obtain the corrected spectrum. Given the pronounced difference in alpha power between groups (Bottari et al., 2016; Ossandón et al., 2023; Pant et al., 2023), we were concerned it might drive differences in the exponent values. Our analysis pipeline had been adapted from previous publications of our group and other labs (Ossandón et al., 2023; Voytek et al., 2015; Waschke et al., 2017).

We have conducted the analysis with and without the exclusion of the alpha range, as well as using the FOOOF toolbox both in the 1-20 Hz and 20-40 Hz ranges (Ossandón et al., 2023). The findings of a steeper slope in the 1-20 Hz range as well as lower alpha power in CC vs SC individuals remained stable. In Ossandón et al., the comparison between the piecewise fits and FOOOF fits led the authors to use the former, as it outperformed the FOOOF algorithm for their data.

- The model fits of the 1/f fitting for EO, EC, and both participant groups should be reported.

In Figure 3 of the manuscript, we depicted the mean spectra and 1/f fits for each group.

In the revised manuscript, we added the fit quality metrics (average R² values > 0.91 for each group and condition) (Methods Page 15, Lines 395-396; Supplementary Material S11) and additionally show individual subjects’ fits (Supplementary Material S11). “

(14) The authors mention:

"The EEG data sets reported here were part of data published earlier (Ossandón et al., 2023; Pant et al., 2023)." Thus, the statement "The group differences for the EEG assessments corresponded to those of a larger sample of CC individuals (n=38) " is a circular argument and should be avoided."

The authors addressed this comment and adjusted the statement. However, I do not understand, why not the full sample published earlier (Ossandón et al., 2023) was used in the current study?

The recording of EEG resting state data stated in 2013, while MRS testing could only be set up by the second half of 2019. Moreover, not all subjects who qualify for EEG recording qualify for being scanned (e.g. due to MRI safety, claustrophobia)

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Author response:

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

eLife assessment

This useful manuscript challenges the utility of current paradigms for estimating brain-age with magnetic resonance imaging measures, but presents inadequate evidence to support the suggestion that an alternative approach focused on predicting cognition is more useful. The paper would benefit from a clearer explication of the methods and a more critical evaluation of the conceptual basis of the different models. This work will be of interest to researchers working on brain-age and related models.

Thank you so much for providing high-quality reviews on our manuscript. We revised the manuscript to address all of the reviewers’ comments and provided full responses to each of the comments below. Importantly, in this revision, we clarified that we did not intend to use Brain Cognition as an alternative approach as mentioned by the editor. This is because, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. Here we made this point more explicit and further stated that the relationship between Brain Cognition and fluid cognition indicates the upper limit of Brain Age’s capability in capturing fluid cognition. By examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age. And such quantification is the third aim of this study.

Reviewer #1 (Public Review):

In this paper, the authors evaluate the utility of brain age derived metrics for predicting cognitive decline by performing a 'commonality' analysis in a downstream regression that enables the different contribution of different predictors to be assessed. The main conclusion is that brain age derived metrics do not explain much additional variation in cognition over and above what is already explained by age. The authors propose to use a regression model trained to predict cognition ('brain cognition') as an alternative suited to applications of cognitive decline. While this is less accurate overall than brain age, it explains more unique variance in the downstream regression.

Importantly, in this revision, we clarified that we did not intend to use Brain Cognition as an alternative approach. This is because, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. Here we made this point more explicit and further stated that the relationship between Brain Cognition and fluid cognition indicates the upper limit of Brain Age’s capability in capturing fluid cognition. By examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age.

REVISED VERSION: while the authors have partially addressed my concerns, I do not feel they have addressed them all. I do not feel they have addressed the weight instability and concerns about the stacked regression models satisfactorily.

Please see our responses to #3 below

I also must say that I agree with Reviewer 3 about the limitations of the brain age and brain cognition methods conceptually. In particular that the regression model used to predict fluid cognition will by construction explain more variance in cognition than a brain age model that is trained to predict age. This suffers from the same problem the authors raise with brain age and would indeed disappear if the authors had a separate measure of cognition against which to validate and were then to regress this out as they do for age correction. I am aware that these conceptual problems are more widespread than this paper alone (in fact throughout the brain age literature), so I do not believe the authors should be penalised for that. However, I do think they can make these concerns more explicit and further tone down the comments they make about the utility of brain cognition. I have indicated the main considerations about these points in the recommendations section below.

Thank you so much for raising this point. We now have the following statement in the introduction and discussion to address this concern (see below).

Briefly, we made it explicit that, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. That is, the relationship between Brain Cognition and fluid cognition indicates the upper limit of Brain Age’s capability in capturing fluid cognition. More importantly, by examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age. And this is the third goal of this present study.

From Introduction:

“Third and finally, certain variation in fluid cognition is related to brain MRI, but to what extent does Brain Age not capture this variation? To estimate the variation in fluid cognition that is related to the brain MRI, we could build prediction models that directly predict fluid cognition (i.e., as opposed to chronological age) from brain MRI data. Previous studies found reasonable predictive performances of these cognition-prediction models, built from certain MRI modalities (Dubois et al., 2018; Pat, Wang, Anney, et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022). Analogous to Brain Age, we called the predicted values from these cognition-prediction models, Brain Cognition. The strength of an out-of-sample relationship between Brain Cognition and fluid cognition reflects variation in fluid cognition that is related to the brain MRI and, therefore, indicates the upper limit of Brain Age’s capability in capturing fluid cognition. This is, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. Consequently, if we included Brain Cognition, Brain Age and chronological age in the same model to explain fluid cognition, we would be able to examine the unique effects of Brain Cognition that explain fluid cognition beyond Brain Age and chronological age. These unique effects of Brain Cognition, in turn, would indicate the amount of co-variation between brain MRI and fluid cognition that is missed by Brain Age.”

From Discussion:

“Third, by introducing Brain Cognition, we showed the extent to which Brain Age indices were not able to capture the variation in fluid cognition that is related to brain MRI. More specifically, using Brain Cognition allowed us to gauge the variation in fluid cognition that is related to the brain MRI, and thereby, to estimate the upper limit of what Brain Age can do. Moreover, by examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age.

From our results, Brain Cognition, especially from certain cognition-prediction models such as the stacked models, has relatively good predictive performance, consistent with previous studies (Dubois et al., 2018; Pat, Wang, Anney, et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022). We then examined Brain Cognition using commonality analyses (Nimon et al., 2008) in multiple regression models having a Brain Age index, chronological age and Brain Cognition as regressors to explain fluid cognition. Similar to Brain Age indices, Brain Cognition exhibited large common effects with chronological age. But more importantly, unlike Brain Age indices, Brain Cognition showed large unique effects, up to around 11%. As explained above, the unique effects of Brain Cognition indicated the amount of co-variation between brain MRI and fluid cognition that was missed by a Brain Age index and chronological age. This missing amount was relatively high, considering that Brain Age and chronological age together explained around 32% of the total variation in fluid cognition. Accordingly, if a Brain Age index was used as a biomarker along with chronological age, we would have missed an opportunity to improve the performance of the model by around one-third of the variation explained.”

This is a reasonably good paper and the use of a commonality analysis is a nice contribution to understanding variance partitioning across different covariates. I have some comments that I believe the authors ought to address, which mostly relate to clarity and interpretation

Reviewer #1 Public Review #1

First, from a conceptual point of view, the authors focus exclusively on cognition as a downstream outcome. I would suggest the authors nuance their discussion to provide broader considerations of the utility of their method and on the limits of interpretation of brain age models more generally.

Thank you for your comments on this issue.

We now discussed the broader consideration in detail:

(1) the consistency between our findings on fluid cognition and other recent works on brain disorders,

(2) the difference between studies investigating the utility of Brain Age in explaining cognitive functioning, including ours and others (e.g., Butler et al., 2021; Cole, 2020, 2020; Jirsaraie, Kaufmann, et al., 2023) and those explaining neurological/psychological disorders (e.g., Bashyam et al., 2020; Rokicki et al., 2021)

and

(3) suggested solutions we and others made to optimise the utility of Brain Age for both cognitive functioning and brain disorders.

From Discussion:

“This discrepancy between the predictive performance of age-prediction models and the utility of Brain Age indices as a biomarker is consistent with recent findings (for review, see Jirsaraie, Gorelik, et al., 2023), both in the context of cognitive functioning (Jirsaraie, Kaufmann, et al., 2023) and neurological/psychological disorders (Bashyam et al., 2020; Rokicki et al., 2021). For instance, combining different MRI modalities into the prediction models, similar to our stacked models, often leads to the highest performance of age-prediction models, but does not likely explain the highest variance across different phenotypes, including cognitive functioning and beyond (Jirsaraie, Gorelik, et al., 2023).”

“There is a notable difference between studies investigating the utility of Brain Age in explaining cognitive functioning, including ours and others (e.g., Butler et al., 2021; Cole, 2020, 2020; Jirsaraie, Kaufmann, et al., 2023) and those explaining neurological/psychological disorders (e.g., Bashyam et al., 2020; Rokicki et al., 2021). We consider the former as a normative type of study and the latter as a case-control type of study (Insel et al., 2010; Marquand et al., 2016). Those case-control Brain Age studies focusing on neurological/psychological disorders often build age-prediction models from MRI data of largely healthy participants (e.g., controls in a case-control design or large samples in a population-based design), apply the built age-prediction models to participants without vs. with neurological/psychological disorders and compare Brain Age indices between the two groups. On the one hand, this means that case-control studies treat Brain Age as a method to detect anomalies in the neurological/psychological group (Hahn et al., 2021). On the other hand, this also means that case-control studies have to ignore under-fitted models when applied prediction models built from largely healthy participants to participants with neurological/psychological disorders (i.e., Brain Age may predict chronological age well for the controls, but not for those with a disorder). On the contrary, our study and other normative studies focusing on cognitive functioning often build age-prediction models from MRI data of largely healthy participants and apply the built age-prediction models to participants who are also largely healthy. Accordingly, the age-prediction models for explaining cognitive functioning in normative studies, while not allowing us to detect group-level anomalies, do not suffer from being under-fitted. This unfortunately might limit the generalisability of our study into just the normative type of study. Future work is still needed to test the utility of brain age in the case-control case.”

“Next, researchers should not select age-prediction models based solely on age-prediction performance. Instead, researchers could select age-prediction models that explained phenotypes of interest the best. Here we selected age-prediction models based on a set of features (i.e., modalities) of brain MRI. This strategy was found effective not only for fluid cognition as we demonstrated here, but also for neurological and psychological disorders as shown elsewhere (Jirsaraie, Gorelik, et al., 2023; Rokicki et al., 2021). Rokicki and colleagues (2021), for instance, found that, while integrating across MRI modalities led to age-prediction models with the highest age-prediction performance, using only T1 structural MRI gave age-prediction models that were better at classifying Alzheimer’s disease. Similarly, using only cerebral blood flow gave age-prediction models that were better at classifying mild/subjective cognitive impairment, schizophrenia and bipolar disorder.

As opposed to selecting age-prediction models based on a set of features, researchers could also select age-prediction models based on modelling methods. For instance, Jirsaraie and colleagues (2023) compared gradient tree boosting (GTB) and deep-learning brain network (DBN) algorithms in building age-prediction models. They found GTB to have higher age-prediction performance but DBN to have better utility in explaining cognitive functioning. In this case, an algorithm with better utility (e.g., DBN) should be used for explaining a phenotype of interest. Similarly, Bashyam and colleagues (2020) built different DBN-based age-prediction models, varying in age-prediction performance. The DBN models with a higher number of epochs corresponded to higher age-prediction performance. However, DBN-based age-prediction models with a moderate (as opposed to higher or lower) number of epochs were better at classifying Alzheimer’s disease, mild cognitive impairment and schizophrenia. In this case, a model from the same algorithm with better utility (e.g., those DBN with a moderate epoch number) should be used for explaining a phenotype of interest. Accordingly, this calls for a change in research practice, as recently pointed out by Jirasarie and colleagues (2023, p7), “Despite mounting evidence, there is a persisting assumption across several studies that the most accurate brain age models will have the most potential for detecting differences in a given phenotype of interest”. Future neuroimaging research should aim to build age-prediction models that are not necessarily good at predicting age, but at capturing phenotypes of interest.”

Reviewer #1 Public Review #2

Second, from a methods perspective, there is not a sufficient explanation of the methodological procedures in the current manuscript to fully understand how the stacked regression models were constructed. I would request that the authors provide more information to enable the reader to better understand the stacked regression models used to ensure that these models are not overfit.

Thank you for allowing us an opportunity to clarify our stacked model. We made additional clarification to make this clearer (see below). We wanted to confirm that we did not use test sets to build a stacked model in both lower and higher levels of the Elastic Net models. Test sets were there just for testing the performance of the models.

From Methods: “We used nested cross-validation (CV) to build these prediction models (see Figure 7). We first split the data into five outer folds, leaving each outer fold with around 100 participants. This number of participants in each fold is to ensure the stability of the test performance across folds. In each outer-fold CV loop, one of the outer folds was treated as an outer-fold test set, and the rest was treated as an outer-fold training set. Ultimately, looping through the nested CV resulted in a) prediction models from each of the 18 sets of features as well as b) prediction models that drew information across different combinations of the 18 separate sets, known as “stacked models.” We specified eight stacked models: “All” (i.e., including all 18 sets of features), “All excluding Task FC”, “All excluding Task Contrast”, “Non-Task” (i.e., including only Rest FC and sMRI), “Resting and Task FC”, “Task Contrast and FC”, “Task Contrast” and “Task FC”. Accordingly, there were 26 prediction models in total for both Brain Age and Brain Cognition.

To create these 26 prediction models, we applied three steps for each outer-fold loop. The first step aimed at tuning prediction models for each of 18 sets of features. This step only involved the outer-fold training set and did not involve the outer-fold test set. Here, we divided the outer-fold training set into five inner folds and applied inner-fold CV to tune hyperparameters with grid search. Specifically, in each inner-fold CV, one of the inner folds was treated as an inner-fold validation set, and the rest was treated as an inner-fold training set. Within each inner-fold CV loop, we used the inner-fold training set to estimate parameters of the prediction model with a particular set of hyperparameters and applied the estimated model to the inner-fold validation set. After looping through the inner-fold CV, we, then, chose the prediction models that led to the highest performance, reflected by coefficient of determination (R2), on average across the inner-fold validation sets. This led to 18 tuned models, one for each of the 18 sets of features, for each outer fold.

The second step aimed at tuning stacked models. Same as the first step, the second step only involved the outer-fold training set and did not involve the outer-fold test set. Here, using the same outer-fold training set as the first step, we applied tuned models, created from the first step, one from each of the 18 sets of features, resulting in 18 predicted values for each participant. We, then, re-divided this outer-fold training set into new five inner folds. In each inner fold, we treated different combinations of the 18 predicted values from separate sets of features as features to predict the targets in separate “stacked” models. Same as the first step, in each inner-fold CV loop, we treated one out of five inner folds as an inner-fold validation set, and the rest as an inner-fold training set. Also as in the first step, we used the inner-fold training set to estimate parameters of the prediction model with a particular set of hyperparameters from our grid. We tuned the hyperparameters of stacked models using grid search by selecting the models with the highest R2 on average across the inner-fold validation sets. This led to eight tuned stacked models.

The third step aimed at testing the predictive performance of the 18 tuned prediction models from each of the set of features, built from the first step, and eight tuned stacked models, built from the second step. Unlike the first two steps, here we applied the already tuned models to the outer-fold test set. We started by applying the 18 tuned prediction models from each of the sets of features to each observation in the outer-fold test set, resulting in 18 predicted values. We then applied the tuned stacked models to these predicted values from separate sets of features, resulting in eight predicted values.

To demonstrate the predictive performance, we assessed the similarity between the observed values and the predicted values of each model across outer-fold test sets, using Pearson’s r, coefficient of determination (R2) and mean absolute error (MAE). Note that for R2, we used the sum of squares definition (i.e., R2 = 1 – (sum of squares residuals/total sum of squares)) per a previous recommendation (Poldrack et al., 2020). We considered the predicted values from the outer-fold test sets of models predicting age or fluid cognition, as Brain Age and Brain Cognition, respectively.”

Note some previous research, including ours (Tetereva et al., 2022), splits the observations in the outer-fold training set into layer 1 and layer 2 and applies the first and second steps to layers 1 and 2, respectively. Here we decided against this approach and used the same outer-fold training set for both first and second steps in order to avoid potential bias toward the stacked models. This is because, when the data are split into two layers, predictive models built for each separate set of features only use the data from layer 1, while the stacked models use the data from both layers 1 and 2. In practice with large enough data, these two approaches might not differ much, as we demonstrated previously (Tetereva et al., 2022).

Reviewer #1 Public Review #3

Please also provide an indication of the different regression strengths that were estimated across the different models and cross-validation splits. Also, how stable were the weights across splits?

The focus of this article is on the predictions. Still, it is informative for readers to understand how stable the feature importance (i.e., Elastic Net coefficients) is. To demonstrate the stability of feature importance, we now examined the rank stability of feature importance using Spearman’s ρ (see Figure 4). Specifically, we correlated the feature importance between two prediction models of the same features, used in two different outer-fold test sets. Given that there were five outer-fold test sets, we computed 10 Spearman’s ρ for each prediction model of the same features. We found Spearman’s ρ to be varied dramatically in both age-prediction (range=.31-.94) and fluid cognition-prediction (range=.16-.84) models. This means that some prediction models were much more stable in their feature importance than others. This is probably due to various factors such as a) the collinearity of features in the model, b) the number of features (e.g., 71,631 features in functional connectivity, which were further reduced to 75 PCAs, as compared to 19 features in subcortical volume based on the ASEG atlas), c) the penalisation of coefficients either with ‘Ridge’ or ‘Lasso’ methods, which resulted in reduction as a group of features or selection of a feature among correlated features, respectively, and d) the predictive performance of the models. Understanding the stability of feature importance is beyond the scope of the current article. As mentioned by Reviewer 1, “The predictions can be stable when the coefficients are not,” and we chose to focus on the prediction in the current article.

Reviewer #1 Public Review #4

Please provide more details about the task designs, MRI processing procedures that were employed on this sample in addition to the regression methods and bias correction methods used. For example, there are several different parameterisations of the elastic net, please provide equations to describe the method used here so that readers can easily determine how the regularisation parameters should be interpreted.

Thank you for the opportunity for us to provide more methodical details.

First, for the task design, we included the following statements:

From Methods:

“HCP-A collected fMRI data from three tasks: Face Name (Sperling et al., 2001), Conditioned Approach Response Inhibition Task (CARIT) (Somerville et al., 2018) and VISual MOTOR (VISMOTOR) (Ances et al., 2009).

First, the Face Name task (Sperling et al., 2001) taps into episodic memory. The task had three blocks. In the encoding block [Encoding], participants were asked to memorise the names of faces shown. These faces were then shown again in the recall block [Recall] when the participants were asked if they could remember the names of the previously shown faces. There was also the distractor block [Distractor] occurring between the encoding and recall blocks. Here participants were distracted by a Go/NoGo task. We computed six contrasts for this Face Name task: [Encode], [Recall], [Distractor], [Encode vs. Distractor], [Recall vs. Distractor] and [Encode vs. Recall].

Second, the CARIT task (Somerville et al., 2018) was adapted from the classic Go/NoGo task and taps into inhibitory control. Participants were asked to press a button to all [Go] but not to two [NoGo] shapes. We computed three contrasts for the CARIT task: [NoGo], [Go] and [NoGo vs. Go].

Third, the VISMOTOR task (Ances et al., 2009) was designed to test simple activation of the motor and visual cortices. Participants saw a checkerboard with a red square either on the left or right. They needed to press a corresponding key to indicate the location of the red square. We computed just one contrast for the VISMOTOR task: [Vismotor], which indicates the presence of the checkerboard vs. baseline.”

Second, for MRI processing procedures, we included the following statements.

From Methods: “HCP-A provides details of parameters for brain MRI elsewhere (Bookheimer et al., 2019; Harms et al., 2018). Here we used MRI data that were pre-processed by the HCP-A with recommended methods, including the MSMALL alignment (Glasser et al., 2016; Robinson et al., 2018) and ICA-FIX (Glasser et al., 2016) for functional MRI. We used multiple brain MRI modalities, covering task functional MRI (task fMRI), resting-state functional MRI (rsfMRI) and structural MRI (sMRI), and organised them into 19 sets of features.”

“ Sets of Features 1-10: Task fMRI contrast (Task Contrast) Task contrasts reflect fMRI activation relevant to events in each task. Bookheimer and colleagues (2019) provided detailed information about the fMRI in HCP-A. Here we focused on the pre-processed task fMRI Connectivity Informatics Technology Initiative (CIFTI) files with a suffix, “_PA_Atlas_MSMAll_hp0_clean.dtseries.nii.” These CIFTI files encompassed both the cortical mesh surface and subcortical volume (Glasser et al., 2013). Collected using the posterior-to-anterior (PA) phase, these files were aligned using MSMALL (Glasser et al., 2016; Robinson et al., 2018), linear detrended (see https://groups.google.com/a/humanconnectome.org/g/hcp-users/c/ZLJc092h980/m/GiihzQAUAwAJ) and cleaned from potential artifacts using ICA-FIX (Glasser et al., 2016).

To extract Task Contrasts, we regressed the fMRI time series on the convolved task events using a double-gamma canonical hemodynamic response function via FMRIB Software Library (FSL)’s FMRI Expert Analysis Tool (FEAT) (Woolrich et al., 2001). We kept FSL’s default high pass cutoff at 200s (i.e., .005 Hz). We then parcellated the contrast ‘cope’ files, using the Glasser atlas (Gordon et al., 2016) for cortical surface regions and the Freesurfer’s automatic segmentation (aseg) (Fischl et al., 2002) for subcortical regions. This resulted in 379 regions, whose number was, in turn, the number of features for each Task Contrast set of features. “

“ Sets of Features 11-13: Task fMRI functional connectivity (Task FC) Task FC reflects functional connectivity (FC ) among the brain regions during each task, which is considered an important source of individual differences (Elliott et al., 2019; Fair et al., 2007; Gratton et al., 2018). We used the same CIFTI file “_PA_Atlas_MSMAll_hp0_clean.dtseries.nii.” as the task contrasts. Unlike Task Contrasts, here we treated the double-gamma, convolved task events as regressors of no interest and focused on the residuals of the regression from each task (Fair et al., 2007). We computed these regressors on FSL, and regressed them in nilearn (Abraham et al., 2014). Following previous work on task FC (Elliott et al., 2019), we applied a highpass at .008 Hz. For parcellation, we used the same atlases as Task Contrast (Fischl et al., 2002; Glasser et al., 2016). We computed Pearson’s correlations of each pair of 379 regions, resulting in a table of 71,631 non-overlapping FC indices for each task. We then applied r-to-z transformation and principal component analysis (PCA) of 75 components (Rasero et al., 2021; Sripada et al., 2019, 2020). Note to avoid data leakage, we conducted the PCA on each training set and applied its definition to the corresponding test set. Accordingly, there were three sets of 75 features for Task FC, one for each task.

Set of Features 14: Resting-state functional MRI functional connectivity (Rest FC) Similar to Task FC, Rest FC reflects functional connectivity (FC ) among the brain regions, except that Rest FC occurred during the resting (as opposed to task-performing) period. HCP-A collected Rest FC from four 6.42-min (488 frames) runs across two days, leading to 26-min long data (Harms et al., 2018). On each day, the study scanned two runs of Rest FC, starting with anterior-to-posterior (AP) and then with posterior-to-anterior (PA) phase encoding polarity. We used the “rfMRI_REST_Atlas_MSMAll_hp0_clean.dscalar.nii” file that was pre-processed and concatenated across the four runs. We applied the same computations (i.e., highpass filter, parcellation, Pearson’s correlations, r-to-z transformation and PCA) with the Task FC.

Sets of Features 15-18: Structural MRI (sMRI)

sMRI reflects individual differences in brain anatomy. The HCP-A used an established pre-processing pipeline for sMRI (Glasser et al., 2013). We focused on four sets of features: cortical thickness, cortical surface area, subcortical volume and total brain volume. For cortical thickness and cortical surface area, we used Destrieux’s atlas (Destrieux et al., 2010; Fischl, 2012) from FreeSurfer’s “aparc.stats” file, resulting in 148 regions for each set of features. For subcortical volume, we used the aseg atlas (Fischl et al., 2002) from FreeSurfer’s “aseg.stats” file, resulting in 19 regions. For total brain volume, we had five FreeSurfer-based features: “FS_IntraCranial_Vol” or estimated intra-cranial volume, “FS_TotCort_GM_Vol” or total cortical grey matter volume, “FS_Tot_WM_Vol” or total cortical white matter volume, “FS_SubCort_GM_Vol” or total subcortical grey matter volume and “FS_BrainSegVol_eTIV_Ratio” or ratio of brain segmentation volume to estimated total intracranial volume.”

Third, for regression methods and bias correction methods used, we included the following statements:

From Methods:

“For the machine learning algorithm, we used Elastic Net (Zou & Hastie, 2005). Elastic Net is a general form of penalised regressions (including Lasso and Ridge regression), allowing us to simultaneously draw information across different brain indices to predict one target variable. Penalised regressions are commonly used for building age-prediction models (Jirsaraie, Gorelik, et al., 2023). Previously we showed that the performance of Elastic Net in predicting cognitive abilities is on par, if not better than, many non-linear and more-complicated algorithms (Pat, Wang, Bartonicek, et al., 2022; Tetereva et al., 2022). Moreover, Elastic Net coefficients are readily explainable, allowing us the ability to explain how our age-prediction and cognition-prediction models made the prediction from each brain feature (Molnar, 2019; Pat, Wang, Bartonicek, et al., 2022) (see below).

Elastic Net simultaneously minimises the weighted sum of the features’ coefficients. The degree of penalty to the sum of the feature’s coefficients is determined by a shrinkage hyperparameter ‘α’: the greater the α, the more the coefficients shrink, and the more regularised the model becomes. Elastic Net also includes another hyperparameter, ‘l1 ratio’, which determines the degree to which the sum of either the squared (known as ‘Ridge’; l1 ratio=0) or absolute (known as ‘Lasso’; l1 ratio=1) coefficients is penalised (Zou & Hastie, 2005). The objective function of Elastic Net as implemented by sklearn (Pedregosa et al., 2011) is defined as:

where X is the features, y is the target, and β is the coefficient. In our grid search, we tuned two Elastic Net hyperparameters: α using 70 numbers in log space, ranging from .1 and 100, and l_1-ratio using 25 numbers in linear space, ranging from 0 and 1.

To understand how Elastic Net made a prediction based on different brain features, we examined the coefficients of the tuned model. Elastic Net coefficients can be considered as feature importance, such that more positive Elastic Net coefficients lead to more positive predicted values and, similarly, more negative Elastic Net coefficients lead to more negative predicted values (Molnar, 2019; Pat, Wang, Bartonicek, et al., 2022). While the magnitude of Elastic Net coefficients is regularised (thus making it difficult for us to interpret the magnitude itself directly), we could still indicate that a brain feature with a higher magnitude weights relatively stronger in making a prediction. Another benefit of Elastic Net as a penalised regression is that the coefficients are less susceptible to collinearity among features as they have already been regularised (Dormann et al., 2013; Pat, Wang, Bartonicek, et al., 2022).

Given that we used five-fold nested cross validation, different outer folds may have different degrees of ‘α’ and ‘l1 ratio’, making the final coefficients from different folds to be different. For instance, for certain sets of features, penalisation may not play a big part (i.e., higher or lower ‘α’ leads to similar predictive performance), resulting in different ‘α’ for different folds. To remedy this in the visualisation of Elastic Net feature importance, we refitted the Elastic Net model to the full dataset without splitting them into five folds and visualised the coefficients on brain images using Brainspace (Vos De Wael et al., 2020) and Nilern (Abraham et al., 2014) packages. Note, unlike other sets of features, Task FC and Rest FC were modelled after data reduction via PCA. Thus, for Task FC and Rest FC, we, first, multiplied the absolute PCA scores (extracted from the ‘components_’ attribute of ‘sklearn.decomposition.PCA’) with Elastic Net coefficients and, then, summed the multiplied values across the 75 components, leaving 71,631 ROI-pair indices. “

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

eLife assessment

This useful manuscript challenges the utility of current paradigms for estimating brain-age with magnetic resonance imaging measures, but presents inadequate evidence to support the suggestion that an alternative approach focused on predicting cognition is more useful. The paper would benefit from a clearer explication of the methods and a more critical evaluation of the conceptual basis of the different models. This work will be of interest to researchers working on brain-age and related models.

Thank you so much for providing high-quality reviews on our manuscript. We revised the manuscript to address all of the reviewers’ comments and provided full responses to each of the comments below. Importantly, in this revision, we clarified that we did not intend to use Brain Cognition as an alternative approach. This is because, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. Here we made this point more explicit and further stated that the relationship between Brain Cognition and fluid cognition indicates the upper limit of Brain Age’s capability in capturing fluid cognition. By examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age. And such quantification is the third aim of this study.

Public Reviews:

Reviewer 1 (Public Review):

In this paper, the authors evaluate the utility of brain-age-derived metrics for predicting cognitive decline by performing a 'commonality' analysis in a downstream regression that enables the different contribution of different predictors to be assessed. The main conclusion is that brain-age-derived metrics do not explain much additional variation in cognition over and above what is already explained by age. The authors propose to use a regression model trained to predict cognition ("brain-cognition") as an alternative suited to applications of cognitive decline. While this is less accurate overall than brain age, it explains more unique variance in the downstream regression.

(1) I thank the authors for addressing many of my concerns with this revision. However, I do not feel they have addressed them all. In particular I think the authors could do more to address the concern I raised about the instability of the regression coefficients and about providing enough detail to determine that the stacked regression models do not overfit.

Thank you Reviewer 1 for the comment. We addressed them in our response to Reviewer 1 Recommendations For The Authors #1 and #2 (see below).

(2) In considering my responses to the authors revision, I also must say that I agree with Reviewer 3 about the limitations of the brain age and brain cognition methods conceptually. In particular that the regression model used to predict fluid cognition will by construction explain more variance in cognition than a brain age model that is trained to predict age. To be fair, these conceptual problems are more widespread than this paper alone, so I do not believe the authors should be penalised for that. However, I would recommend to make these concerns more explicit in the manuscript

Thank you Reviewer 1 for the comment. We addressed them in our response to Reviewer 1 Recommendations For The Authors #3 (see below).

Reviewer 2 (Public Review):

In this study, the authors aimed to evaluate the contribution of brain-age indices in capturing variance in cognitive decline and proposed an alternative index, brain-cognition, for consideration.

The study employs suitable methods and data to address the research questions, and the methods and results sections are generally clear and easy to follow.

I appreciate the authors' efforts in significantly improving the paper, including some considerable changes, from the original submission. While not all reviewer points were tackled, the majority of them were adequately addressed. These include additional analyses, more clarity in the methods and a much richer and nuanced discussion. While recognising the merits of the revised paper, I have a few additional comments.

(1) Perhaps it would help the reader to note that it might be expected for brain-cognition to account for a significantly larger variance (11%) in fluid cognition, in contrast to brain-age. This stems from the fact that the authors specifically trained brain-cognition to predict fluid cognition, the very variable under consideration. In line with this, the authors later recommend that researchers considering the use of brain-age should evaluate its utility using a regression approach. The latter involves including a brain index (e.g. brain-cognition) previously trained to predict the regression's target variable (e.g. fluid cognition) alongside a brain-age index (e.g., corrected brain-age gap). If the target-trained brain index outperforms the brain-age metric, it suggests that relying solely on brain-age might not be the optimal choice. Although not necessarily the case, is it surprising for the target-trained brain index to demonstrate better performance than brain-age? This harks back to the broader point raised in the initial review: while brain-age may prove useful (though sometimes with modest effect sizes) across diverse outcomes as a generally applicable metric, a brain index tailored for predicting a specific outcome, such as brain-cognition in this case, might capture a considerably larger share of variance in that specific context but could lack broader applicability. The latter aspect needs to be empirically assessed.

Thank you so much for raising this point. Reviewer 1 (Public Review #2/Recommendations For The Authors #3) and Reviewer 3 (Recommendations for the Authors #1) made a similar observation. We now made changes to the introduction and discussion to address this concern (please see our responses to Reviewer 1 Recommendations For The Authors #3 below).

Briefly, as in our 2nd revision, we did not intend to compare Brain Age with Brain Cognition since, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. Here we made this point more explicit and further stated that the relationship between Brain Cognition and fluid cognition indicates the upper limit of Brain Age’s capability in capturing fluid cognition. By examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age. And such quantification is the third aim of this study.

(2) Furthermore, the discussion pertaining to training brain-age models on healthy populations for subsequent testing on individuals with neurological or psychological disorders seems somewhat one-sided within the broader debate. This one-sidedness might potentially confuse readers. It is worth noting that the choice to employ healthy participants in the training model is likely deliberate, serving as a norm against which atypical populations are compared. To provide a more comprehensive understanding, referencing Tim Hans's counterargument to Bashyam's perspective could offer a more complete view (https://academic.oup.com/brain/article/144/3/e31/6214475?login=false).

Thank you Reviewer 2 for bringing up this issue. We have now revised the paragraph in question and added nuances on the usage of Brain Age for normative vs. case-control studies. We also cited Tim Hahn’s article that explained the conceptual foundation of the use of Brain Age in case-control studies. Please see below. Additionally, we also made a statement about our study not being able to address issues about the case-control studies directly in the newly written conclusion (see Reviewer 3 Recommendations for the Authors #3).

Discussion:

“There is a notable difference between studies investigating the utility of Brain Age in explaining cognitive functioning, including ours and others (e.g., Butler et al., 2021; Cole, 2020, 2020; Jirsaraie et al., 2023) and those explaining neurological/psychological disorders (e.g., Bashyam et al., 2020; Rokicki et al., 2021). We consider the former as a normative type of study and the latter as a case-control type of study (Insel et al., 2010; Marquand et al., 2016). Those case-control Brain Age studies focusing on neurological/psychological disorders often build age-prediction models from MRI data of largely healthy participants (e.g., controls in a case-control design or large samples in a population-based design), apply the built age-prediction models to participants without vs. with neurological/psychological disorders and compare Brain Age indices between the two groups. On the one hand, this means that case-control studies treat Brain Age as a method to detect anomalies in the neurological/psychological group (Hahn et al., 2021). On the other hand, this also means that case-control studies have to ignore under-fitted models when applied prediction models built from largely healthy participants to participants with neurological/psychological disorders (i.e., Brain Age may predict chronological age well for the controls, but not for those with a disorder). On the contrary, our study and other normative studies focusing on cognitive functioning often build age-prediction models from MRI data of largely healthy participants and apply the built age-prediction models to participants who are also largely healthy. Accordingly, the age-prediction models for explaining cognitive functioning in normative studies, while not allowing us to detect group-level anomalies, do not suffer from being under-fitted. This unfortunately might limit the generalisability of our study into just the normative type of study. Future work is still needed to test the utility of brain age in the case-control case.”

(3) Overall, this paper makes a significant contribution to the field of brain-age and related brain indices and their utility.

Thank you for the encouragement.

Reviewer 3 (Public Review):

The main question of this article is as follows: "To what extent does having information on brain-age improve our ability to capture declines in fluid cognition beyond knowing a person's chronological age?" This question is worthwhile, considering that there is considerable confusion in the field about the nature of brain-age.

(1) Thank you to the authors for addressing so many of my concerns with this revision. There are a few points that I feel still need addressing/clarifying related to 1) calculating brain cognition, 2) the inevitability of their results, and 3) their continued recommendation to use brain-age metrics.

Thank you Reviewer 3 for the comment. We addressed them in our response to Reviewer 3 Recommendations For The Authors #1-3 (see below).

Recommendations for the authors:

Reviewer 1 (Recommendations For The Authors):

(1) I do not feel the authors have fully addressed the concern I raised about the stacked regression models. Despite the new figure, it is still not entirely clear what the authors are using as the training set in the final step. To be clear, the problem occurs because of the parameters, not the hyperparameters (which the authors now state that they are optimising via nested grid search). in other words, given a regression model y = X*beta, if the X are taken to be predictions from a lower level regression model, then they contain information that is derived from both the training set at the test set for the model that this was trained on. If the split is the same (i.e. the predictions are derived on the same test set as is being used at the second level), then this can lead to overfitting. It is not clear to me whether the authors have done this or not. Please provide additional detail to clarify this point.

Thank you for allowing us an opportunity to clarify our stacked model. We wanted to confirm that we did not use test sets to build a stacked model in both lower and higher levels of the Elastic Net models. Test sets were there just for testing the performance of the models. We made additional clarification to make this clearer (see below). Let us explain what we did and provide the rationales below.

From Methods:

“We used nested cross-validation (CV) to build these prediction models (see Figure 7). We first split the data into five outer folds, leaving each outer fold with around 100 participants. This number of participants in each fold is to ensure the stability of the test performance across folds. In each outer-fold CV loop, one of the outer folds was treated as an outer-fold test set, and the rest was treated as an outer-fold training set. Ultimately, looping through the nested CV resulted in a) prediction models from each of the 18 sets of features as well as b) prediction models that drew information across different combinations of the 18 separate sets, known as “stacked models.” We specified eight stacked models: “All” (i.e., including all 18 sets of features), “All excluding Task FC”, “All excluding Task Contrast”, “Non-Task” (i.e., including only Rest FC and sMRI), “Resting and Task FC”, “Task Contrast and FC”, “Task Contrast” and “Task FC”. Accordingly, there were 26 prediction models in total for both Brain Age and Brain Cognition.

To create these 26 prediction models, we applied three steps for each outer-fold loop. The first step aimed at tuning prediction models for each of 18 sets of features. This step only involved the outer-fold training set and did not involve the outer-fold test set. Here, we divided the outer-fold training set into five inner folds and applied inner-fold CV to tune hyperparameters with grid search. Specifically, in each inner-fold CV, one of the inner folds was treated as an inner-fold validation set, and the rest was treated as an inner-fold training set. Within each inner-fold CV loop, we used the inner-fold training set to estimate parameters of the prediction model with a particular set of hyperparameters and applied the estimated model to the inner-fold validation set. After looping through the inner-fold CV, we, then, chose the prediction models that led to the highest performance, reflected by coefficient of determination (R2), on average across the inner-fold validation sets. This led to 18 tuned models, one for each of the 18 sets of features, for each outer fold.

The second step aimed at tuning stacked models. Same as the first step, the second step only involved the outer-fold training set and did not involve the outer-fold test set. Here, using the same outer-fold training set as the first step, we applied tuned models, created from the first step, one from each of the 18 sets of features, resulting in 18 predicted values for each participant. We, then, re-divided this outer-fold training set into new five inner folds. In each inner fold, we treated different combinations of the 18 predicted values from separate sets of features as features to predict the targets in separate “stacked” models. Same as the first step, in each inner-fold CV loop, we treated one out of five inner folds as an inner-fold validation set, and the rest as an inner-fold training set. Also as in the first step, we used the inner-fold training set to estimate parameters of the prediction model with a particular set of hyperparameters from our grid. We tuned the hyperparameters of stacked models using grid search by selecting the models with the highest R2 on average across the inner-fold validation sets. This led to eight tuned stacked models.

The third step aimed at testing the predictive performance of the 18 tuned prediction models from each of the set of features, built from the first step, and eight tuned stacked models, built from the second step. Unlike the first two steps, here we applied the already tuned models to the outer-fold test set. We started by applying the 18 tuned prediction models from each of the sets of features to each observation in the outer-fold test set, resulting in 18 predicted values. We then applied the tuned stacked models to these predicted values from separate sets of features, resulting in eight predicted values.

To demonstrate the predictive performance, we assessed the similarity between the observed values and the predicted values of each model across outer-fold test sets, using Pearson’s r, coefficient of determination (R2) and mean absolute error (MAE). Note that for R2, we used the sum of squares definition (i.e., R2 = 1 – (sum of squares residuals/total sum of squares)) per a previous recommendation (Poldrack et al., 2020). We considered the predicted values from the outer-fold test sets of models predicting age or fluid cognition, as Brain Age and Brain Cognition, respectively.”

Author response image 1.

Diagram of the nested cross-validation used for creating predictions for models of each set of features as well as predictions for stacked models.

Note some previous research, including ours (Tetereva et al., 2022), splits the observations in the outer-fold training set into layer 1 and layer 2 and applies the first and second steps to layers 1 and 2, respectively. Here we decided against this approach and used the same outer-fold training set for both first and second steps in order to avoid potential bias toward the stacked models. This is because, when the data are split into two layers, predictive models built for each separate set of features only use the data from layer 1, while the stacked models use the data from both layers 1 and 2. In practice with large enough data, these two approaches might not differ much, as we demonstrated previously (Tetereva et al., 2022).

(2) I also do not feel the authors have fully addressed the concern I raised about stability of the regression coefficients over splits of the data. I wanted to see the regression coefficients, not the predictions. The predictions can be stable when the coefficients are not.

The focus of this article is on the predictions. Still, as pointed out by reviewer 1, it is informative for readers to understand how stable the feature importance (i.e., Elastic Net coefficients) is. To demonstrate the stability of feature importance, we now examined the rank stability of feature importance using Spearman’s ρ (see Figure 4). Specifically, we correlated the feature importance between two prediction models of the same features, used in two different outer-fold test sets. Given that there were five outer-fold test sets, we computed 10 Spearman’s ρ for each prediction model of the same features. We found Spearman’s ρ to be varied dramatically in both age-prediction (range=.31-.94) and fluid cognition-prediction (range=.16-.84) models. This means that some prediction models were much more stable in their feature importance than others. This is probably due to various factors such as a) the collinearity of features in the model, b) the number of features (e.g., 71,631 features in functional connectivity, which were further reduced to 75 PCAs, as compared to 19 features in subcortical volume based on the ASEG atlas), c) the penalisation of coefficients either with ‘Ridge’ or ‘Lasso’ methods, which resulted in reduction as a group of features or selection of a feature among correlated features, respectively, and d) the predictive performance of the models. Understanding the stability of feature importance is beyond the scope of the current article. As mentioned by Reviewer 1, “The predictions can be stable when the coefficients are not,” and we chose to focus on the prediction in the current article.

Author response image 2.

Stability of feature importance (i.e., Elastic Net Coefficients) of prediction models. Each dot represents rank stability (reflected by Spearman’s ρ) in the feature importance between two prediction models of the same features, used in two different outer-fold test sets. Given that there were five outer-fold test sets, there were 10 Spearman’s ρs for each prediction model. The numbers to the right of the plots indicate the mean of Spearman’s ρ for each prediction model.

(3) I also must say that I agree with Reviewer 3 about the limitations of the brain-age and brain-cognition methods conceptually. In particular that the regression model used to predict fluid cognition will by construction explain more variance in cognition than a brain-age model that is trained to predict age. This suffers from the same problem the authors raise with brain-age and I agree that this would probably disappear if the authors had a separate measure of cognition against which to validate and were then to regress this out as they do for age correction. I am aware that these conceptual problems are more widespread than this paper alone (in fact throughout the brain-age literature), so I do not believe the authors should be penalised for that. However, I do think they can make these concerns more explicit and further tone down the comments they make about the utility of brain-cognition.

Thank you so much for raising this point. Reviewer 2 (Public Review #1) and Reviewer 3 (Recommendations for the Authors #1) made a similar observation. We now made changes to the introduction and discussion to address this concern (see below).

Briefly, we made it explicit that, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. That is, the relationship between Brain Cognition and fluid cognition indicates the upper limit of Brain Age’s capability in capturing fluid cognition. More importantly, by examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age. And this is the third goal of this present study.

From Introduction:

“Third and finally, certain variation in fluid cognition is related to brain MRI, but to what extent does Brain Age not capture this variation? To estimate the variation in fluid cognition that is related to the brain MRI, we could build prediction models that directly predict fluid cognition (i.e., as opposed to chronological age) from brain MRI data. Previous studies found reasonable predictive performances of these cognition-prediction models, built from certain MRI modalities (Dubois et al., 2018; Pat et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022). Analogous to Brain Age, we called the predicted values from these cognition-prediction models, Brain Cognition. The strength of an out-of-sample relationship between Brain Cognition and fluid cognition reflects variation in fluid cognition that is related to the brain MRI and, therefore, indicates the upper limit of Brain Age’s capability in capturing fluid cognition. This is, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. Consequently, if we included Brain Cognition, Brain Age and chronological age in the same model to explain fluid cognition, we would be able to examine the unique effects of Brain Cognition that explain fluid cognition beyond Brain Age and chronological age. These unique effects of Brain Cognition, in turn, would indicate the amount of co-variation between brain MRI and fluid cognition that is missed by Brain Age.”

From Discussion:

“Third, by introducing Brain Cognition, we showed the extent to which Brain Age indices were not able to capture the variation in fluid cognition that is related to brain MRI. More specifically, using Brain Cognition allowed us to gauge the variation in fluid cognition that is related to the brain MRI, and thereby, to estimate the upper limit of what Brain Age can do. Moreover, by examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age.

From our results, Brain Cognition, especially from certain cognition-prediction models such as the stacked models, has relatively good predictive performance, consistent with previous studies (Dubois et al., 2018; Pat et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022). We then examined Brain Cognition using commonality analyses (Nimon et al., 2008) in multiple regression models having a Brain Age index, chronological age and Brain Cognition as regressors to explain fluid cognition. Similar to Brain Age indices, Brain Cognition exhibited large common effects with chronological age. But more importantly, unlike Brain Age indices, Brain Cognition showed large unique effects, up to around 11%. As explained above, the unique effects of Brain Cognition indicated the amount of co-variation between brain MRI and fluid cognition that was missed by a Brain Age index and chronological age. This missing amount was relatively high, considering that Brain Age and chronological age together explained around 32% of the total variation in fluid cognition. Accordingly, if a Brain Age index was used as a biomarker along with chronological age, we would have missed an opportunity to improve the performance of the model by around one-third of the variation explained.”

Reviewer #3 (Recommendations For The Authors):

Thank you to the authors for addressing so many of my concerns with this revision. There are a few points that I feel still need addressing/clarifying related to: 1) calculating brain cognition, 2) the inevitability of their results, and 3) their continued recommendation to use brain age metrics.

(1) I understand your point here. I think the distinction is that it is fine to build predictive models, but then there is no need to go through this intermediate step of "brain-cognition". Just say that brain features can predict cognition XX well, and brain-age (or some related metric) can predict cognition YY well. It creates a confusing framework for the reader that can lead them to believe that "brain-cognition" is not just a predicted value of fluid cognition from a model using brain features to predict cognition. While you clearly state that that is in fact what it is in the text, which is a huge improvement, I do not see what is added by going through brain-cognition instead of simply just obtaining a change in R2 where the first model uses brain features alone to predict cognition, and the second adds on brain-age (or related metrics), or visa versa, depending on the question. Please do this analysis, and either compare and contrast it with going through "brain-cognition" in your paper, or switch to this analysis, as it more directly addresses the question of the incremental predictive utility of brain-age above and beyond brain features.

Thank you so much for raising this point. Reviewer 1 (Public Review #2/Recommendations For The Authors #3) and Reviewer 2 (Public Review #1) made a similar observation. We now made changes to the introduction and discussion to address this concern (see our responses to Reviewer 1 Recommendations For The Authors #3 above).

Briefly, as in our 2nd revision, we made it explicitly clear that we did not intend to compare Brain Age with Brain Cognition since, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. And, by examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age.

We have thought about changing the name Brain Cognition into something along the lines of “predicted values of prediction models predicting fluid cognition based on brain MRI.” However, this made the manuscript hard to follow, especially with the commonality analyses. For instance, the sentence, “Here, we tested Brain Cognition’s unique effects in multiple regression models with a Brain Age index, chronological age and Brain Cognition as regressors to explain fluid cognition” would become “Here, we tested predicted values of prediction models predicting fluid cognition based on brain MRI unique effects in multiple regression models with a Brain Age index, chronological age and predicted values of prediction models predicting fluid cognition based on brain MRI as regressors to explain fluid cognition.” We believe, given our additional explanation (see our responses to Reviewer 1 Recommendations For The Authors #3 above), readers should understand what Brain Cognition is, and that we did not intend to compare Brain Age and Brain Cognition directly.

As for the suggested analysis, “obtaining a change in R2 where the first model uses brain features alone to predict cognition, and the second adds on brain-age (or related metrics), or visa versa,” we have already done this in the form of commonality analysis (Nimon et al., 2008) (see Figure 7 below). That is, to obtain unique and common effects of the regressors, we need to look at all of the possible changes in R2 when all possible subsets of regressors were excluded or included, see equations 12 and 13 below.

From Methods:

“Similar to the above multiple regression model, we had chronological age, each Brain Age index and Brain Cognition as the regressors for fluid cognition:

Fluid Cognitioni = β0 + β1 Chronological Agei + β2 Brain Age Indexi,j + β3 Brain Cognitioni + εi, (12)

Applying the commonality analysis here allowed us, first, to investigate the addictive, unique effects of Brain Cognition, over and above chronological age and Brain Age indices. More importantly, the commonality analysis also enabled us to test the common, shared effects that Brain Cognition had with chronological age and Brain Age indices in explaining fluid cognition. We calculated the commonality analysis as follows (Nimon et al., 2017):

Unique Effectchronological age = ΔR2chronological age = R2chronological age, Brain Age index, Brain Cognition – R2 Brain Age index, Brain Cognition

Unique EffectBrain Age index = ΔR2Brain Age index = R2chronological age, Brain Age index, Brain Cognition – R2 chronological age, Brain Cognition

Unique EffectBrain Cognition = ΔR2Brain Cognition = R2chronological age, Brain Age index, Brain Cognition – R2 chronological age, Brain Age Index

Common Effectchronological age, Brain Age index = R2chronological age, Brain Cognition + R2 Brain Age index, Brain Cognition – R2 Brain Cognition – R2chronological age, Brain Age index, Brain Cognition

Common Effectchronological age, Brain Cognition = R2chronological age, Brain Age Index + R2 Brain Age index, Brain Cognition – R2 Brain Age Index – R2chronological age, Brain Age index, Brain Cognition

Common Effect Brain Age index, Brain Cognition = R2chronological age, Brain Age Index + R2 chronological age, Brain Cognition – R2 chronological age – R2chronological age, Brain Age index, Brain Cognition

Common Effect chronological age, Brain Age index, Brain Cognition = R2 chronological age + R2 Brain Age Index + R2 Brain Cognition – R2chronological age, Brain Age Index – R2 chronological age, Brain Cognition – R2 Brain Age Index, Brain Cognition – R2chronological age, Brain Age index, Brain Cognition , (13)”

(2) I agree that the solution is not to exclude age as a covariate, and that there is a big difference between inevitable and obvious. I simply think a further discussion of the inevitability of the results would be clarifying for the readers. There is a big opportunity in the brain-age literature to be as direct as possible about why you are finding what you are finding. People need to know not only what you found, but why you found what you found.

Thank you. We agreed that we need to make this point more explicit and direct. In the revised manuscript, we had the statements in both Introduction and Discussion (see below) about the tight relationship between Brain Age and chronological age by design, making the small unique effects of Brain Age inevitable.

Introduction:

“Accordingly, by design, Brain Age is tightly close to chronological age. Because chronological age usually has a strong relationship with fluid cognition, to begin with, it is unclear how much Brain Age adds to what is already captured by chronological age.“

Discussion:

“First, Brain Age itself did not add much more information to help us capture fluid cognition than what we had already known from a person’s chronological age. This can clearly be seen from the small unique effects of Brain Age indices in the multiple regression models having Brain Age and chronological age as the regressors. While the unique effects of some Brain Age indices from certain age-prediction models were statistically significant, there were all relatively small. Without Brain Age indices, chronological age by itself already explained around 32% of the variation in fluid cognition. Including Brain Age indices only added around 1.6% at best. We believe the small unique effects of Brain Age were inevitable because, by design, Brain Age is tightly close to chronological age. Therefore, chronological age and Brain Age captured mostly a similar variation in fluid cognition.

Investigating the simple regression models and the commonality analysis between each Brain Age index and chronological age provided additional insights….”

(3) I believe it is very important to critically examine the use of brain-age and related metrics. As part of this process, I think we should be asking ourselves the following questions (among others): Why go through age prediction? Wouldn't the predictions of cognition (or another variable) using the same set of brain features always be as good or better? You still have not justified the use of brain-age. As I said before, if you are going to continue to recommend the use of brain-age, you need a very strong argument for why you are recommending this. What does it truly add? Otherwise, temper your statements to indicate possible better paths forward.

Thank you Reviewer 3 for making an argument against the use of Brain Age. We largely agree with you. However, our work only focuses on one phenotype, fluid cognition, and on the normative situation (i.e., not having a case vs control group). As Reviewer 2 pointed out, Brain Age might still have utility in other cases, not studied here. Still, future studies that focus on other phenotypes may consider using our approach as a template to test the utility of Brain Age in other situations. We added the conclusion statement to reflect this.

From Discussion:

“Altogether, we examined the utility of Brain Age as a biomarker for fluid cognition. Here are the three conclusions. First, Brain Age failed to add substantially more information over and above chronological age. Second, a higher ability to predict chronological age did not correspond to a higher utility to capture fluid cognition. Third, Brain Age missed up to around one-third of the variation in fluid cognition that could have been explained by brain MRI. Yet, given our focus on fluid cognition, future empirical research is needed to test the utility of Brain Age on other phenotypes, especially when Brain Age is used for anomaly detection in case-control studies (e.g., Bashyam et al., 2020; Rokicki et al., 2021). We hope that future studies may consider applying our approach (i.e., using the commonality analysis that includes predicted values from a model that directly predicts the phenotype of interest) to test the utility of Brain Age as a biomarker for other phenotypes.”

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Author Response

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

Reviewer #1 (Recommendations for The Authors):

To hopefully contribute to more strongly support the conclusions of the manuscript, I am including a series of concerns regarding the experiments, as well as some recommendations that could be followed to address these issues:

(1) The Q-nMT bundle is largely unaffected by the nocodazole treatment in most phases during its formation. However, cells were only treated with nocodazole for a very short period of time (15 min). Have the authors analyzed Q-nMT stability after longer nocodazole exposures? Is a similar treatment enough to depolymerize the mitotic spindle? This result could be further substantiated by treatment with other MT-depolymerizing agents. Furthermore, the dynamicity of the Q-nMT bundle could be ideally also assessed by other techniques, such as FRAP.

The experiments suggested by the reviewer have been published in our previous paper (Laporte et al, JCB 2013). In this previous study, we presented data demonstrating the resistance of the Q-nMT bundle to several MT poisons: TBZ, benomyl, MBC (Sup Fig 2D) and to an increasing amount of nocodazole after a 90 min treatment (Sup Fig2E). These published figures are provided below.

Author response image 1.

The nMT array contains highly stable MTS. (A) Variation Of nuclear MT length in function Of time (second) in proliferating cells. Cells express GFP•Tubl (green) and Nup2•RFP (red). Bars, 2 pm. N = l, n is indicated. (B) Variation of the nMT array length in function of time measured for BirnlGFP—expressing cells In = 161, for 6-d•old Dad2GFP—expressing cells In = 171, for Stu2GFP—expressing cells (n = 17), and 6•d-old Nuf2• GFP—expressing cells (n = 17). Examples Of corresponding time lapse are shown. Time is in minutes experiments). Bar, 2 pm. (CJ Nuf2•GFP dots detected along nMT array (arrow) are immobile. Several time lapse images of cells are shown. Time is in minutes. gar, 2 pm _ MT organizations in proliferating cells and 4-d•old quiescent cells before and after a 90-min treatment With indicated drugs. Bar, 2 pm. (E) MT organizations in Sci-old quiescent cells before and after a 90min treatment With increasing concentrations Of nocodazole.

In the same article, we showed that Q-nMT bundles resist a 3h nocodazole treatment, while all MT structures assembled in proliferating cells, including mitotic spindle, vanished (see Fig 2E below). In addition, in our previous article, FRAP experiments were provided in Fig 2D.

Author response image 2.

The nuclear array is composed of stable MTS. Variation of the length in function of time of (A) aMTs in proliferating cells, (B) nMT array in quiescent cells (7 d), and the two MT structures in early quiescent cells (4 d). White arrows point ot dynamic aMTs. In A—C, N = 2, n is indicated ID) FRAP on 7-d-old quiescent cells. White arrows point to bleach areas. Error bars are SEM. In A—D. time is in seconds. (E) nMT array is not affected by nocodazole treatment. Before and various times after carbon exhaustion (red dashed line), cells were incubated for 3 h with 22.5 pg/pL nocodozole and then imaged. The corresponding control experiment is shown in Fig I A. In all panels, cells expressing GFP-TtJbl (green) and Nup2-RFP (red) are shown; bars, 2 pm.

This previous study was mentioned in the introduction and is now re-cited at the beginning of the results section (line 107-108).

As expected from our previous study, when proliferating cells were treated with Noc (30 µg/ml) in the same conditions as in Fig1, most of the short and the long mitotic spindles vanished after a 15 min treatment as shown in the graph below.

Author response image 3.

Proliferating cells expressing NOf2=GFP and mTQZ-TUb1 (00—2) were treated or not With NOC (30vgfmI) for 15 min.% Of cells With detectable MT and representative cells are shown. Khi-teet values are indicated. Bar: 2 pm,

(2) The graph in Figure 1B is somewhat confusing. Is the X-axis really displaying the length of the MTs as stated in the legend? If so, one would expect to see a displacement of the average MT length of the population as cells progress from phase II to phase III, as previously demonstrated in Figure 1A. Likewise, no data points would be anticipated for those phases in which the MT length is 0 or close to 0. Moreover, when the length of half pre-anaphase mitotic spindle was measured as a control, how can one get MT lengths that are equal or close to 0 in these cells? The length of the pre-anaphase spindle is between 2-4 um, so MT length values should range from 1 to 2 um if half the spindle is measured.

The graph in Fig1B represents the fluorescence intensity (a proxy for the Q-nMT bundle thickness) along the Q-nMT bundle length.

Fluorescence intensity is measured along a “virtual line” that starts 0,5 µm before the extremity of the QnMT bundle that is in contact with the SPB. In other words, we aligned all intensity measurements at the fluorescence increasing onset on the SPB side. We arbitrarily set the ‘zero’ at 0,5um before the fluorescence increased onset. That is why the fluorescence intensity is zero between 0 and 0,5 µm – The X-axis represents this virtual line, the 0 being set 0,5 µm before the Q-nMT bundle extremity on the SPB side. This virtual line allows us to standardize our “thickness” measurements for all Q-nMT bundles.

Using this standardization, it is clear that the length of the Q-nMT bundles increased from phase II to III (see the red arrow). Yet, as in phase II, Q-nMT bundles are not yet stable, their lengths are shorter in phase II than in phase II after a Noc treatment (compare the end of the orange line and the end of the blue line in phase II).

Author response image 4.

This is now explained in details in the Material and Methods section (line 539-545).

This is the same for the inset of Fig 1B and in Sup Fig 1A, in which we measured fluorescence intensity along the halfmitotic spindle just as we did for MT bundle. The X-axis represent a virtual line along the mitotic spindle, starting 0,5 µm before the SBP spindle extremity.

Author response image 5.

(3) Microtubules seem to locate next to or to extend beyond the nucleus in the control cells (DMSO) in Figure 1H. Since both nuclear MTs and cytoplasmic MTs emanate from the SPBs, it would have been desirable to display the morphology of the nucleus when possible. Moreover, since the nucleus is a tridimensional structure, it would also be advisable to image different Z-sections.

Analysis demonstrating that Q-nMT bundles are located inside the nucleus have been provided in our previous paper (Laporte et al, JCB 2013). In this article most of the images are maximal projections of Z-stacks in which the nuclear envelope is visualized via Nup2-RFP (see Fig1 of Laporte et al, JCB 2013 as an example below).

Author response image 6.

MTsare organized as a nuclear array in quiescent cells. (A) MT reorganization upon quiescence entry. Cells expressing GFP-Tub1 (green) and Nup2RFP (red) are shown. Glucose exhaustion is indicated as a red dashed line. Quiescent cells dl expressing Tub I-RFP and either Spc72GFP,

In Laporte et al, JCB 2013, we also provided EM analysis both in cryo and immune-gold (Fig 1E below).

Author response image 7.

(top) or coexpr;sse8 with Tub I-RFP (bottom). Arrows point dot along the nMT array. Bars: (A—C)) 2 pm. (E) AMT arroy visualized in WT cells by EMI Yellow arrows, MTS; red arrowheads, nuclear membrane; pink arrow, SPB. Insets: nMT cut transversally. Bar, 100 nm.

(4) Movies depicting the process of Q-nMT bundle formation in live cells would have been really informative to more precisely evaluate the MT dynamics. Likewise, together with still images (Fig 1D and Supp. Fig. 1D), movies depicting the changes in the localization of Nuf2-GFP would have further facilitated the analysis of this process.

In a new Sup Fig 1E, we now provide images of Q-nMT bundle formation initiation in phase I, in which it can be observed that Nuf2-GFP accompanies the growth of MT (mTQZ-TUB1) at the onset of Q-nMT bundle formation. Unfortunately, it is technically very challenging to follow the entire process of Q-nMT bundle formation in individual cells, as it takes > 48h. Indeed, for movies longer than 24h, on both microscope pads or specific microfluidic devices (Jacquel, et al, eLife 2021), phototoxicity and oxygen availability become problematic and affect cells’ viability.

(5) Western blot images displaying the relative protein levels for mTQZ-Tub1 and of the ADH2 promoter-driven mRuby-Tub1 at the different time points should be included to more strongly support the conclusion that new tubulin molecules are introduced in the Q-nMT bundle only after phase I. It is worth noting, in this sense, that the percentage of cells with 2 colors Q-nMT bundle is analyzed only 1 hour after expression of mRuby-Tub1 was induced for phase I cells, but after 24 hours for phase II cells.<br /> We have modified Fig 1F and now provide images of cells after 3, 6 and 24h after glucose exhaustion and the corresponding percentage of cells displaying Q-nMT bundle with the two colors. We also now provide a western blot in Sup Fig 1H using specific antibodies against mTQZ (anti-GFP) and mRuby (anti-RFP).

(6) In order to demonstrate that Q-nMT formation is an active process induced by a transient signal and that the Q-nMT bundle is required for cell survival, the authors treated cells with nocodazole for 24 h (Fig 1H and Supp Fig 1K). Both events, however, could be associated with the toxic effects of the extremely prolonged nocodazole treatment leading to cell death.

We have treated 5 days old cells for 24h with 30 µg/ml Noc. We then washed the drug and transferred the cells into a glucose free medium. We then followed both cell survival, using methylene blue, and the cell’s capacity to form a colony after refeeding. In these conditions, we did not observe any toxic effect of the nocodazole. This result is now provided in Sup Fig 1L and discussed line 172-176.

(7) The "Tub1-only" mutant displays shorter but stable Q-nMT bundles in phase II, although they are thinner than in wild-type cells. What happens in the "Tub3-only" mutant, which also has beta-tubulin levels similar to wild-type cells (Supp. Fig. 2B)?

In order to measure Q-nMT bundle length and thickness, we used Tub1 fused to GFP. This cannot be done in a Tub3-only mutant. Yet, we have measured Q-nMT bundle length in Tub3-only cells using Bim1-3GFP as a MT marker (as in Laporte et al, JCB 2013). As shown in the figure below, Q-nMT bundles were shorter in Tub3-only cells than in WT cells whatever the phase.

Author response image 8.

We do not know if this effect is directly linked to the absence of Tub1 or if it is very indirect and for example due to the fact that Tub1 and Tub3 interact differently with Bim1 or other proteins that are involved in Q-nMT bundle stabilization. As we cannot give a clear interpretation for that result, we decided not to present those data in our manuscript.

(8) Why were wild-type and ndc80-1 cells imaged after a 20 min nocodazole treatment to evaluate the role of KT-MT attachments in Q-nMT bundle formation (Fig 3A)? Importantly, this experiment is also missing a control in which Q-nMT length is analyzed in both wild-type and ndc80-1 cells at 25ºC instead of 37ºC.

In this experiment, we used nocodazole to test both the formation and the stability of the Q-nMT bundle. Fig 3A shows MT length distribution in WT (grey) and ndc80-1 (violet) cells expressing mTQZTub1 (green) and Nuf2-GFP (red), shifted to 37 °C at the onset of glucose exhaustion and kept at this non-permissive temperature for 12 or 96 h then treated with Noc. The control experiment was provided in Sup Fig 3B. Indeed, this figure shows MT length in WT (grey) and ndc80-1 (violet) expressing mTQZ-Tub1 (green) and Nuf2-GFP (red) grown for 4 d (96h) at 25 °C, and treated or not with Noc. This is now indicated in the text line 216 and in the figure legend line 976

Author response image 9.

(9) As a general comment linked to the previous concern, it is striking that in many instances, Q-nMT bundle length is measured after nocodazole treatment without any evident reason to do this and without displaying the results in untreated cells as a control. If nocodazole is used, the authors should explicitly indicate it and state the reason for it.

We provide control experiments without nocodazole for all of the figures. For the sake of figure clarity, for Fig.3A the control without the drug is in Sup. Fig. 3B, for Fig. 3B it is shown in Sup. Fig. 3D, for Fig. 4B, it is shown in Sup. Fig 4A. This is now stated in the text and in the figure legend: for Fig. 3A: line 216 and in the figure legend line 976; for Fig. 3B: line 222 and figure legend line 984; for Fig. 4B: line 280 and in the figure legend line 1017.

The only figures where the untreated cells are not shown is for Fig 1D since the goal of the experiment is to make dynamic MTs shorten.

In Fig. 5C and Sup. Fig. 5D to F, we used nocodazole to get rid of dynamic cytoplasmic MTs that form upon quiescence exit in order to facilitate Q-nMT bundle measurement. This was explained in our previous study (Laporte et al, JCB 2013). We now mention it in the figure legends, see for example Fig. 5 legend line 1054.

(10) Ipl1 inactivation using the ipl1-1 thermosensitive allele impedes Q-nMT bundle formation. The inhibitor-sensitive ipl1-as1 allele could have been further used to show whether this depends on its kinase activity, also avoiding the need to increase the temperature, which affects MT dynamics. As suggested, we have used the ipl1-5as allele. We have thus modified Fig 3B and now show that is it indeed the Ipl1 kinase activity that is required for Q-nMT bundle formation initiation (line 222). In any case, it is surprising that deletion of SLI15 does not affect Q-nMT formation (in fact, MT length is even larger), despite the fact that Sli15, which localizes and activates Ipl1, is present at the Q-nMT (Fig 3C). Likewise, deletion of BIR1 has barely any effect on MT length after 4 days in quiescence (Fig 3D). Do the previous observations mean that Ipl1 role is CPC-independent? Does the lack of Sli15 or Bir1 aggravate the defect in Q-nMT formation of ipl1-1 cells at non-permissive or semi-permissive temperature?

Thanks to the Reviewer’s comments, we have re-checked our sli15Δ strain and found that it was accumulating suppressors very rapidly. To circumvent this problem, we utilized the previously described sli15-3 strain (Kim et al, JCB 1999). We found that sli15-3 was synthetic lethal with both ipl1-1, ipl1-2 (as described in Kim et al, JCB 1999) and with ipl1-as5, preventing us from addressing the CPC dependence of the Ipl1 effect asked by the Reviewer. However, using the sli15-3 strain, we now show that inactivation of Sli15 upon glucose exhaustion does prevent Q-nMT bundle formation (See new Sup Fig 3F and the text line 226-227).

(11) Lack of both Bir1 and Bim1 act in a synergistic way with regard to the defect in Q-nMT bundle formation. Although the absence of both Sli15 and Bim1 is proposed to lead to a similar defect, this is not sustained by the data provided, particularly in the absence of nocodazole treatment (Supp. Fig 3E).

Deletion of bir1 alone has only a subtle effect on Q-nMT bundle length in the absence of Noc, yet in bir1Δ cells, Q-nMT bundles are sensitive to Noc. Deletion of BIM1 (bim1Δ) aggravates this phenotype (Fig. 3D). As mentioned above, Q-nMT bundle formation is impaired in sli15-3 cells. In our hands, and as expected from (Zimnaik et al, Cur Biol 2012), this allele is synthetic lethal with bim1Δ.

On the other hand, the simultaneous lack of Bir1 and Bim1 drastically reduces the viability of cells in quiescence and this is proposed to be evidence supporting that KT-MT attachments are critical for QnMT bundle assembly (Supp Fig 3G). However, similarly to what was indicated previously for the 24 h nocodazole treatment, here again, the lack of viability could be originated by other reasons that are associated with the lack of Bir1 and Bim1 and not necessarily with problems in Q-nMT formation. In fact, the viability defect of cells lacking Bir1 and Bim1 is similar to that of cells only lacking Bir1 (Supp Fig 3G).

We have previously shown that many mutants impaired for Q-nMT bundle formation (dyn1Δ, nip100Δ etc) have a reduced viability in quiescence (Laporte et al, JCB 2013). In the current study, a very strong phenotype is observed for other mutants impaired for Q-nMT bundle formation such as bim1Δ bir1Δ cells, but also for slk19Δ bim1Δ.

Importantly, as shown in the new Sup Fig 1L, in WT cells treated with Noc upon entry into quiescence, a treatment that prevents Q-nMT formation, showed a reduced viability, while a Noc treatment that does not affect Q-nMT bundle formation, i.e. a treatment in late quiescence, has no effect on cell survival. This solid set of data point to a clear correlation between the ability of cells to assemble a Q-nMT bundle and their ability to survive in quiescence. Yet, of course, we cannot formally exclude that in all these mutants, the reduction of cell viability in quiescence is due to another reason.

(12) Both Mam1 and Spo13 are, to my knowledge, meiosis-specific proteins. It is therefore surprising that mutants in these proteins have an effect on MT bundle formation (Fig 3G-H, Supp. Fig. 3G). Are Mam1 and Spo13 also expressed during quiescence? Transcription of MAM1 or SPO13 does not seem to be induced by glucose depletion in previously published microarray experiments, but if Mam1 are Spo13 are expressed in quiescent cells, the authors should show this together with their results.<br /> Indeed, it is interesting to notice that Mam1 and Spo13 are involved in both meiosis and Q-nMT bundle formation. As suggested by the Reviewer we have performed western blots in order to address the expression of those proteins in proliferation and quiescence (4d). We tagged Spo13 with either GFP, HA or Myc but none of the fusion proteins were functional. Yet, as shown in the new Sup Fig 3I, Mam1-GFP, Csm1-GFP and Lsr4-GFP were expressed both in proliferation and quiescence.

(13) In the laser ablation experiments that demonstrate that KT-MT attachments are not needed in order to maintain Q-nMT bundles once formed, anaphase spindles of proliferating cells were cut as a control (Supp. Fig 3I). However, late anaphase cells have already segregated the chromosomes, which lie next to the SPBs (this can be evidenced by looking at Dad2-GFP localization in Supp. Fig 3I), so that only interpolar MTs are severed in these experiments. The authors should have instead used metaphase cells as a control, since chromosomes are maintained at the spindle midzone and the length and width of the metaphase spindle is more similar to that of the Q-nMT bundle.

We have tried to “cut” short metaphase spindles, but as they are < 1 µm, after the laser pulse, it is difficult to verify that spindles are indeed cut and not solely “bleached”. Furthermore, after the cut, the remaining MT structure that is detectable is very short, and we are not confident in our length measurements. Yet, this type of experiment has been done in S. pombe (Khodjakov et al, Cur Biol 2004 and Zareiesfandabadi et al, Biophys. J. 2022). In these articles the authors have demonstrated that after a cut, metaphase spindles are unstable and rapidly shrink through the action of Kinesin14 and dynein. This is now mentioned in the text line 265.

(14) In the experiment that shows that cycloheximide prevents Q-nMT disassembly after quiescence exit, and therefore that this process requires de novo protein synthesis (Fig. 5A), cells are indicated to express only Spc42-RFP and Nuf2-GFP. However, Stu2-GFP images are also shown next to the graph and, according to the figure legend, it was indeed Stu2-GFP that was used to measure individual QnMT bundles in cells treated with cycloheximide. In the graph, additionally, time t=0 represents the onset of MT bundle depolymerization, but Q-nMT bundle disassembly does not take place after cycloheximide treatment. The authors should clarify these aspects of the experiment.

Following the Reviewer’s suggestion, to clarify these aspects we have split Fig. 5A into 2 panels.

Finally, some minor issues are:

(1) The text should be checked for proper spelling and grammar.

We have done our best.

(2) In some instances, there is no indication of how many cells were imaged and analyzed.

We now provide all these details either in the figure itself or in the figure legend.

(3) Besides the Q-nMT bundle, it is sometimes noticeable an additional strong cytoplasmic fluorescent signal in cells that express mTQZ-Tub1 and/or mRuby-Tub1 (e.g., Figs 1F, 1H and, particularly, Supp Fig 1H). What is the nature of these cytoplasmic MT structures?

We did mention this observation in the material and methods section (see line 526-528). This signal is a background fluorescence signal detected with our long pass GFP filter. It is not GFP as it is “yellowish” when we view it via the microscope oculars. This background signal can also be observed in quiescent WT cells that do not express any GFP. We do not know what molecule could be at the origin of that signal but it may be derivative of an adenylic metabolite that accumulates in quiescence and could be fluorescent in the 550nm –ish wavelength, but this is pure speculation.

(4) It is remarkable that a 20-30% decrease in tubulin levels had such a strong impact on the assembly of the Q-nMT bundle (Supp. Fig. 2). Can this phenotype be recovered by increasing the amount of tubulin in the mutants impaired for tubulin folding?

Yes, this is astonishing, but we believe our data are very solid since we observed that with both tub3Δ and in all the tubulin folding mutants we have tested (See Sup. Fig. 2). To answer Reviewer’s question, we would need to increase the amount of properly folded tubulin, in a tubulin folding mutant. One way to try to do that would be to find suppressors of GIM mutations, but this is a lengthy process that we feel would not add much strength to this conclusion.

(5) The graphs displaying the length of the Q-nMT bundle in several mutants in microtubule motors throughout a time course are presented in a different manner than in previous experiments, with data points for individual cells being only shown for the most extreme values (Fig 4C, 4H). It would be advisable, for the sake of comparison, to unify the way to represent the data.

We have now unified the way we present our figures.

(6) How was the exit from quiescence established in the experiments evaluating Q-nMT disassembly? How synchronous is quiescence exit in the whole population of cells once they are transferred to a rich medium?

We set the “zero” time upon cell refeeding with new medium. In fact, quiescence exit is NOT synchronous. We have reported this in previous publications, with the best description of this phenomena being in Laporte et al, MIC 2017 . <br /> The figures below are the same data but on the left graph, the kinetic is aligned upon SPB separation onset, while on the right graph (Fig 5A), it is aligned on MT shrinking onset.

Author response image 10.

We can add this piece of data in a Sup Figure if the Reviewer believes it is important.

Reviewer #2 (Recommendations For The Authors):

General:

• In general, more precise language that accurately describes the experiments would improve the text. <br /> We have tried to do our best to improve the text.

• The authors should clearly define what they mean by an active process and provide context to support this statement regarding the Q-nMT.

We have strived to clarify this point in the text (see paragraph form line 146 to 178).

• It is reasonable to assume that structures composed of microtubules are dynamic during the assembly process. The authors should clarify what they mean by "stable by default i.e., intrinsically stable." Do they mean that when Q-nMT assembly starts, it will proceed to completion regardless of a change in condition?

We mean that in phase I the Q-nMT bundle is stabilized as it grows and that stabilization is concomitant with polymerization. By contrast, MTs polymerized during phase II are not stabilized upon elongation beyond the phase I polymer, and get stabilized later, in a separate phase (i.e. in phase III). We hope to have clarified this point in the text (see line 108-110).

• In lines 33-34, the authors claim that the Q-nMT bundle functions as a "sort of checkpoint for cell cycle resumption." This wording is imprecise, and more significantly the authors do not provide evidence supporting a direct role for Q-nMT in a quiescence checkpoint that inhibits re-entry into the cell cycle.

We have softened and clarified the text in the abstract (see line 29-30)., in the introduction (line 101104), in the result section (line 331-332) and in the discussion (line 426-430).

• Many statements are qualitative and subjective. Quantitative statements supported by the results should be used where possible, and if not possible restated or removed.

We provide statistical data analysis for all the figures.

• The number of hours after glucose exhaustion used for each phase varies between assays. This is likely a logistical issue but should be explained.

This is indeed a logistical issue and when pertinent, it is explained in the text.

• It would be interesting to address how this process occurs in diploids. Do they form a Q-nMT? How does this relate to the decision to enter meiosis?

Diploid cells enter meiosis when they are starved for nitrogen. Upon glucose exhaustion diploids do form a Q-nMT bundle. This is shown and measured in the new Sup Fig1C. In fact, in diploids, Q-nMT bundles are thicker than in haploid cells.

• It would be interesting to address how the timescale of this process compares to the types of nutrient stress yeast would be exposed to in the environment.

We have transferred proliferating yeast cells to water, to try to mimic what could happen when yeast cells face rain in the wild. As shown below, they do form a Q-nMT bundle that becomes nocodazole resistant after 30h. This data is now provided in the new Sup Fig 1D.

• It is recommended that the authors use FRAP experiments to directly measure the stability of the QnMT bundles.

This experiment was published in (Laporte et al, 2013). Please see response to Reviewer #1.

• In many cases, the description of the experimental methods lacks sufficient detail to evaluate the approach or for independent verification of results.

We have strived to provide a more detailed material and methods section, as well as more detailed figure legends and statistical informations.

Specific comments on figures:

• In Figure 1 c), what do the polygons represent? They do not contain all the points of the associated colour.

The polygon represented the area of distribution of 90% of the data points. As they did not significantly add to the data presentation they have been removed.

• In Figure 2 a), is the use of two different sets of markers to control for the effect of the markers on microtubule dynamics?

Yes, we are always concerned about the influence of GFP on our results, so very often we replicate our experiments with different fluorescent proteins or even with different proteins tagged with GFP. This is now mentioned in the text (line 184-186).

• Is it accurate to say (line 201, figure 3 a)) that no Q-nMT bundles were detected in ndc80-1 cells shifted to 37 degrees, or are they just shorter?

As shown in Fig 3A, in ndc80-1 cells, most of the MT structures that we measured are below 0,5um. This has been re-phrased in the text (line 214-215).

• Lines 265-269, figure 4 b), how can the phenotype observed in cin8∆ cells be explained given the low abundance of Cin8 that is detected in quiescent cells?

Faint fluorescence signal is not synonymous of an absence of function. As shown in Sup Fig 4B, we do detect Cin8-GFP in quiescent cells.

• Quantification is needed in Figure 4 panels c) and h).

Fig 4C and 4H have been changed and quantification are provided in the figure legend.

Reviewer #3 (Recommendations For The Authors):

A few points should be addressed for clarity:

(1) Sup. Fig. 1K: are only viable cells used for the colony-forming assay? How were these selected? If not, the assay would just measure survival (as in the viability assay).

Yes, only viable cells were selected for the colony forming assay. We used methylene blue to stain dead cells. Then, we used a micromanipulation instrument (Singer Spore Play) that is commonly used for tetrad dissection to select “non blue cells” and position them on a plate (as we do with spores). Each micromanipulated cell is then allowed to grow on the plate and we count colonies (see picture in Sup Fig 1L right panel). This was described in Laporte et al, JCB 2011. We have added that piece of information in the legend (line 1129-1130) and in the M&M section (line 580-586).

(2) Could Tub3 have a role in phase I? It is not clear why the authors conclude involvement only in phase II.

As it can be seen in Fig 2D, MT bundle length and thickness are quite similar in WT and Tub1-only cells in phase I, indicating that the absence of Tub3 as no effect in phase I. In Tub1-only cells, MT bundles are thinner in both phase II and phase III, yet, they get fully stabilized in phase III. Thus, the effect of Tub3 is largely specific to the nucleation/elongation of phase II MTs. We hope to have clarified that point in the text (line 203-207).

(3) Quantifications, statistics: for all quantifications, the authors should clearly state the number of experiments (replicates), and number of cells used in each, and what number was used for statistics. For all quantifications in cells, it seems that the values from the total number of cells across different experiments were plotted and used for statistics. This is not very useful and results in extremely small p values. I assume that the values for individual cells were obtained from multiple, independent experiments. Unless there are technical limitations that allow only a very small sample size (not the case here for most experiments), for experiments involving treatments the authors should determine values for each experiment and show statistics for comparison between experiments rather than individual cells pooled from multiple experiments.

All the experiments have been done at least in replicate. In the new Fig. 1A, we now display each independent experiment with a specific color code. For Fig 2B and 2C we now provide the data obtained for each separate experiment in Sup Fig 2C. Additional details about quantifications and statistics are provided in the M&M section or in the specific figure legends.

Author response:

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

Public Reviews:

Reviewer #1:

Summary:

The work by Combrisson and colleagues investigates the degree to which reward and punishment learning signals overlap in the human brain using intracranial EEG recordings. The authors used information theory approaches to show that local field potential signals in the anterior insula and the three sub regions of the prefrontal cortex encode both reward and punishment prediction errors, albeit to different degrees. Specifically, the authors found that all four regions have electrodes that can selectively encode either the reward or the punishment prediction errors. Additionally, the authors analyzed the neural dynamics across pairs of brain regions and found that the anterior insula to dorsolateral prefrontal cortex neural interactions were specific for punishment prediction errors whereas the ventromedial prefrontal cortex to lateral orbitofrontal cortex interactions were specific to reward prediction errors. This work contributes to the ongoing efforts in both systems neuroscience and learning theory by demonstrating how two differing behavioral signals can be differentiated to a greater extent by analyzing neural interactions between regions as opposed to studying neural signals within one region.

Strengths:

The experimental paradigm incorporates both a reward and punishment component that enables investigating both types of learning in the same group of subjects allowing direct comparisons.

The use of intracranial EEG signals provides much needed insight into the timing of when reward and punishment prediction errors signals emerge in the studied brain regions.

Information theory methods provide important insight into the interregional dynamics associated with reward and punishment learning and allows the authors to assess that reward versus punishment learning can be better dissociated based on interregional dynamics over local activity alone.

We thank the reviewer for this accurate summary. Please find below our answers to the weaknesses raised by the reviewer.

Weaknesses:

The analysis presented in the manuscript focuses solely on gamma band activity. The presence and potential relevance of other frequency bands is not discussed. It is possible that slow oscillations, which are thought to be important for coordinating neural activity across brain regions could provide additional insight.

We thank the reviewer for pointing us to this missing discussion in the first version of the manuscript. We now made this point clearer in the Methods sections entitled “iEEG data analysis” and “Estimate of single-trial gamma-band activity”:

“Here, we focused solely on broadband gamma for three main reasons. First, it has been shown that the gamma band activity correlates with both spiking activity and the BOLD fMRI signals (Lachaux et al., 2007; Mukamel et al., 2004; Niessing et al., 2005; Nir et al., 2007), and it is commonly used in MEG and iEEG studies to map task-related brain regions (Brovelli et al., 2005; Crone et al., 2006; Vidal et al., 2006; Ball et al., 2008; Jerbi et al., 2009; Darvas et al., 2010; Lachaux et al., 2012; Cheyne and Ferrari, 2013; Ko et al., 2013). Therefore, focusing on the gamma band facilitates linking our results with the fMRI and spiking literatures on probabilistic learning. Second, single-trial and time-resolved high-gamma activity can be exploited for the analysis of cortico-cortical interactions in humans using MEG and iEEG techniques (Brovelli et al., 2015; 2017; Combrisson et al., 2022). Finally, while previous analyses of the current dataset (Gueguen et al., 2021) reported an encoding of PE signals at different frequency bands, the power in lower frequency bands were shown to carry redundant information compared to the gamma band power.”

The data is averaged across all electrodes which could introduce biases if some subjects had many more electrodes than others. Controlling for this variation in electrode number across subjects would ensure that the results are not driven by a small subset of subjects with more electrodes.

We thank the reviewer for raising this important issue. We would like to point out that the gamma activity was not averaged across bipolar recordings within an area, nor measures of connectivity. Instead, we used a statistical approach proposed in a previous paper that combines non-parametric permutations with measures of information (Combrisson et al., 2022). As we explain in the “Statistical analysis” section, mutual information (MI) is estimated between PE signals and single-trial modulations in gamma activity separately for each contact (or for each pair of contacts). Then, a one-sample t-test is computed across all of the recordings of all subjects to form the effect size at the group-level. We will address the point of the electrode number in our answer below.

The potential variation in reward versus punishment learning across subjects is not included in the manuscript. While the time course of reward versus punishment prediction errors is symmetrical at the group level, it is possible that some subjects show faster learning for one versus the other type which can bias the group average. Subject level behavioral data along with subject level electrode numbers would provide more convincing evidence that the observed effects are not arising from these potential confounds.

We thank the reviewer for the two points raised. We performed additional analyses at the single-participant level to address the issues raised by the reviewer. We should note, however, that these results are descriptive and cannot be generalized to account for population-level effects. As suggested by the reviewer, we prepared two new figures. The first supplementary figure summarizes the number of participants that had iEEG contacts per brain region and pair of brain regions (Fig. S1A in the Appendix). It can be seen that the number of participants sampled in different brain regions is relatively constant (left panel) and the number of participants with pairs of contacts across brain regions is relatively homogeneous, ranging from 7 to 11 (right panel). Fig. S1B shows the number of bipolar derivations per subject and per brain region.

Author response image 1.

Single subject anatomical repartition. (A) Number of unique subject per brain region and per pair of brain regions (B) Number of bipolar derivations per subject and per brain region

The second supplementary figure describes the estimated prediction error for rewarding and punishing trials for each subject (Fig. S2). The single-subject error bars represent the 95th percentile confidence interval estimated using a bootstrap approach across the different pairs of stimuli presented during the three to six sessions. As the reviewer anticipated, there are indeed variations across subjects, but we observe that RPE and PPE are relatively symmetrical, even at the subject level, and tend toward zero around trial number 10. These results therefore corroborate the patterns observed at the group-level.

Author response image 2.

Single-subject estimation of predictions errors. Single-subject trial-wise reward PE (RPE - blue) and punishment PE (PPE - red), ± 95% confidence interval.

Finally, to assess the variability of local encoding of prediction errors across participants, we quantified the proportion of subjects having at least one significant bipolar derivation encoding either the RPE or PPE (Fig. S4). As expected, we found various proportions of unique subjects with significant R/PPE encoding per region. The lowest proportion was achieved in the ventromedial prefrontal cortex (vmPFC) and lateral orbitofrontal cortex (lOFC) for encoding PPE and RPE, respectively, with approximately 30% of the subjects having the effect. Conversely, we found highly reproducible encodings in the anterior insula (aINS) and dorsolateral prefrontal cortex (dlPFC) with a maximum of 100% of the 9 subjects having at least one bipolar derivation encoding PPE in the dlPFC.

Author response image 3.

Taken together, we acknowledge a certain variability per region and per condition. Nevertheless, the results presented in the supplementary figures suggest that the main results do not arise from a minority of subjects.

We would like to point out that in order to assess across-subject variability, a much larger number of participants would have been needed, given the low signal-to-noise ratios observed at the single-participant level. We thus prefer to add these results as supplementary material in the Appendix, rather than in the main text.

It is unclear if the findings in Figures 3 and 4 truly reflect the differential interregional dynamics in reward versus punishment learning or if these results arise as a statistical byproduct of the reward vs punishment bias observed within each region. For instance, the authors show that information transfer from anterior insula to dorsolateral prefrontal cortex is specific to punishment prediction error. However, both anterior insula and dorsolateral prefrontal cortex have higher prevalence of punishment prediction error selective electrodes to begin with. Therefore the findings in Fig 3 may simply be reflecting the prevalence of punishment specificity in these two regions above and beyond a punishment specific neural interaction between the two regions. Either mathematical or analytical evidence that assesses if the interaction effect is simply reflecting the local dynamics would be important to make this result convincing.

This is an important point that we partly addressed in the manuscript. More precisely, we investigated whether the synergistic effects observed between the dlPFC and vmPFC encoding global PEs (Fig. 5) could be explained by their respective local specificity. Indeed, since we reported larger proportions of recordings encoding the PPE in the dlPFC and the RPE in the vmPFC (Fig. 2B), we checked whether the synergy between dlPFC and vmPFC could be mainly due to complementary roles where the dlPFC brings information about the PPE only and the vmPFC brings information to the RPE only. To address this point, we selected PPE-specific bipolar derivations from the dlPFC and RPE-specific from the vmPFC and, as the reviewer predicted, we found synergistic II between the two regions probably mainly because of their respective specificity. In addition, we included the II estimated between non-selective bipolar derivations (i.e. recordings with significant encoding for both RPE and PPE) and we observed synergistic interactions (Fig. 5C and Fig. S9). Taken together, the local specificity certainly plays a role, but this is not the only factor in defining the type of interactions.

Concerning the interaction information results (II, Fig. 3), several lines of evidence suggest that local specificity cannot account alone for the II effects. For example, the local specificity for PPE is observed across all four areas (Fig. 2A) and the percentage of bipolar derivations displaying an effect is large (equal or above 10%) for three brain regions (aINS, dlPLF and lOFC). If the local specificity were the main driving cause, we would have observed significant redundancy between all pairs of brain regions. On the other hand, the interaction between the aINS and lOFC displayed no significant redundant effect (Fig. 3B). Another example is the result observed in lOFC: approximately 30% of bipolar derivations display a selectivity for PPE (Fig. 2B, third panel from the left), but do not show clear signs of redundant encoding at the level of within-area interactions (Fig. 3A, bottom-left panel). Similarly, the local encoding for RPE is observed across all four brain regions (Fig. 2A) and the percentage of bipolar derivations displaying an effect is large (equal or above 10%) for three brain regions (aINS, dlPLF and vmPFC). Nevertheless, significant between-regions interactions have been observed only between the lOFC and vmPFC (Fig. 3B bottom right panel).

To further support the reasoning, we performed a simulation to show that it is possible to observe synergistic interactions between two regions with the same specificity. As an example, we may consider one region locally encoding early trials of RPE and a second region encoding the late trials of the RPE. Combining the two with the II would lead to synergistic interactions, because each one of them carries information that is not carried by the other. To illustrate this point, we simulated the data of two regions (x and y). To simulate redundant interactions (first row), each region receives a copy of the prediction (one-to-all) and for the synergy (second row), x and y receive early and late PE trials, respectively (all-to-one). This toy example illustrates that the local specificity is not the only factor determining the type of their interactions. We added the following result to the Appendix.

Author response image 4.

Local specificity does not fully determine the type of interactions. Within-area local encoding of PE using the mutual information (MI, in bits) for regions X and Y and between-area interaction information (II, in bits) leading to (A) redundant interactions and (B) synergistic interactions about the PE

Regarding the information transfer results (Fig. 4), similar arguments hold and suggest that the prevalence is not the main factor explaining the arising transfer entropy between the anterior insula (aINS) and dorsolateral prefrontal cortex (dlPFC). Indeed, the lOFC has a strong local specificity for PPE, but the transfer entropy between the lOFC and aINS (or dlPFC) is shown in Fig. S7 does not show significant differences in encoding between PPE and RPE.

Indeed, such transfer can only be found when there is a delay between the gamma activity of the two regions. In this example, the transfer entropy quantifies the amount of information shared between the past activity of the aINS and the present activity of the dlPFC conditioned on the past activity of the dlPFC. The conditioning ensures that the present activity of the dlPFC is not only explained by its own past. Consequently, if both regions exhibit various prevalences toward reward and punishment but without delay (i.e. at the same timing), the transfer entropy would be null because of the conditioning. As a fact, between 10 to -20% of bipolar recordings show a selectivity to the reward PE (represented by a proportion of 40-60% of subjects, Fig.S4). However, the transfer entropy estimated from the aINS to the dlPFC across rewarding trials is flat and clearly non-significant. If the transfer entropy was a byproduct of the local specificity then we should observe an increase, which is not the case here.

Reviewer #2:

Summary:

Reward and punishment learning have long been seen as emerging from separate networks of frontal and subcortical areas, often studied separately. Nevertheless, both systems are complimentary and distributed representations of rewards and punishments have been repeatedly observed within multiple areas. This raised the unsolved question of the possible mechanisms by which both systems might interact, which this manuscript went after. The authors skillfully leveraged intracranial recordings in epileptic patients performing a probabilistic learning task combined with model-based information theoretical analyses of gamma activities to reveal that information about reward and punishment was not only distributed across multiple prefrontal and insular regions, but that each system showed specific redundant interactions. The reward subsystem was characterized by redundant interactions between orbitofrontal and ventromedial prefrontal cortex, while the punishment subsystem relied on insular and dorsolateral redundant interactions. Finally, the authors revealed a way by which the two systems might interact, through synergistic interaction between ventromedial and dorsolateral prefrontal cortex.

Strengths:

Here, the authors performed an excellent reanalysis of a unique dataset using innovative approaches, pushing our understanding on the interaction at play between prefrontal and insular cortex regions during learning. Importantly, the description of the methods and results is truly made accessible, making it an excellent resource to the community.

This manuscript goes beyond what is classically performed using intracranial EEG dataset, by not only reporting where a given information, like reward and punishment prediction errors, is represented but also by characterizing the functional interactions that might underlie such representations. The authors highlight the distributed nature of frontal cortex representations and propose new ways by which the information specifically flows between nodes. This work is well placed to unify our understanding of the complementarity and specificity of the reward and punishment learning systems.

We thank the reviewer for the positive feedback. Please find below our answers to the weaknesses raised by the reviewer.

Weaknesses:

The conclusions of this paper are mostly supported by the data, but whether the findings are entirely generalizable would require further information/analyses.

First, the authors found that prediction errors very quickly converge toward 0 (less than 10 trials) while subjects performed the task for sets of 96 trials. Considering all trials, and therefore having a non-uniform distribution of prediction errors, could potentially bias the various estimates the authors are extracting. Separating trials between learning (at the start of a set) and exploiting periods could prove that the observed functional interactions are specific to the learning stages, which would strengthen the results.

We thank the reviewer for this question. We would like to note that the probabilistic nature of the learning task does not allow a strict distinction between the exploration and exploitation phases. Indeed, the probability of obtaining the less rewarding outcome was 25% (i.e., for 0€ gain in the reward learning condition and -1€ loss in the punishment learning condition). Thus, participants tended to explore even during the last set of trials in each session. This is evident from the average learning curves shown in Fig. 1B of (Gueguen et al., 2021). Learning curves show rates of correct choice (75% chance of 1€ gain) in the reward condition (blue curves) and incorrect choice (75% chance of 1€ loss) in the punishment condition (red curves).

For what concerns the evolution of PEs, as reviewer #1 suggested, we added a new figure representing the single-subject estimates of the R/PPE (Fig S2). Here, the confidence interval is obtained across all pairs of stimuli presented during the different sessions. We retrieved the general trend of the R/PPE converging toward zero around 10 trials. Both average reward and punishment prediction errors converge toward zero in approximately 10 trials, single-participant curves display large variability, also at the end of each session. As a reminder, the 96 trials represent the total number of trials for one session for the four pairs and the number of trials for each stimulus was only 24.

Author response image 5.

Single-subject estimation of predictions errors. Single-subject trial-wise reward PE (RPE - blue) and punishment PE (PPE - red), ± 95% confidence interval

However, the convergence of the R/PPE is due to the average across the pairs of stimuli. In the figure below, we superimposed the estimated R/PPE, per pair of stimuli, for each subject. It becomes very clear that high values of PE can be reached, even for late trials. Therefore, we believe that the split into early/late trials because of the convergence of PE is far from being trivial.

Author response image 6.

Single-subject estimation of predictions errors per pair of stimuli. Single-subject trial-wise reward PE (RPE - blue) and punishment PE (PPE - red)

Consequently, nonzero PRE and PPE occur during the whole session and separating trials between learning (at the start of a set) and exploiting periods, as suggested by the reviewer, does not allow a strict dissociation between learning vs no-learning. Nevertheless, we tested the analysis proposed by the reviewer, at the local level. We splitted the 24 trials of each pair of stimuli into early, middle and late trials (8 trials each). We then reproduced Fig. 2 by computing the mutual information between the gamma activity and the R/PPE for subsets of trials: early (first row) and late trials (second row). We retrieved significant encoding of both R/PPE in the aINS, dlPFC and lOFC in both early and late trials. The vmPFC also showed significant encoding of both during early trials. The only difference emerges in the late trials of the vmPFC where we found a strong encoding of the RPE only. It should also be noted that here since we are sub-selecting the trials, the statistical analyses are only performed using a third of the trials.

Taken together, the combination of high values of PE achieved even for late trials and the fact that most of the findings are reproduced even with a third of the trials does not justify the split into early and late trials here. Crucially, this latest analysis confirms that the neural correlates of learning that we observed reflect PE signals rather than early versus late trials in the session.

Author response image 7.

MI between gamma activity and R/PPE using early and late trials. Time courses of MI estimated between the gamma power and both RPE (blue) and PPE (red) using either early or late trials (first and second row, respectively). Horizontal thick lines represent significant clusters of information (p<0.05, cluster-based correction, non-parametric randomization across epochs).

Importantly, it is unclear whether the results described are a common feature observed across subjects or the results of a minority of them. The authors should report and assess the reliability of each result across subjects. For example, the authors found RPE-specific interactions between vmPFC and lOFC, even though less than 10% of sites represent RPE or both RPE/PPE in lOFC. It is questionable whether such a low proportion of sites might come from different subjects, and therefore whether the interactions observed are truly observed in multiple subjects. The nature of the dataset obviously precludes from requiring all subjects to show all effects (given the known limits inherent to intracerebral recording in patients), but it should be proven that the effects were reproducibly seen across multiple subjects.

We thank the reviewer for this remark that has also been raised by the first reviewer. This issue was raised by the first reviewer. Indeed, we added a supplementary figure describing the number of unique subjects per brain region and per pair of brain regions (Fig. S1A) such as the number of bipolar derivations per region and per subject (Fig. S1B).

Author response image 8.

Single subject anatomical repartition. (A) Number of unique subject per brain region and per pair of brain regions (B) Number of bipolar derivations per subject and per brain region

Regarding the reproducibility of the results across subjects for the local analysis (Fig. 2), we also added the instantaneous proportion of subjects having at least one bipolar derivation showing a significant encoding of the RPE and PPE (Fig. S4). We found a minimum proportion of approximately 30% of unique subjects having the effect in the lOFC and vmPFC, respectively with the RPE and PPE. On the other hand, both the aINS and dlPFC showed between 50 to 100% of the subjects having the effect. Therefore, local encoding of RPE and PPE was never represented by a single subject.

Author response image 9.

Similarly, we performed statistical analysis on interaction information at the single-subject level and counted the proportion of unique subjects having at least one pair of recordings with significant redundant and synergistic interactions about the RPE and PPE (Fig. S5). Consistently with the results shown in Fig. 3, the proportions of significant redundant and synergistic interactions are negative and positive, respectively. For the within-regions interactions, approximately 60% of the subjects with redundant interactions are about R/PPE in the aINS and about the PPE in the dlPFC and 40% about the RPE in the vmPFC. For the across-regions interactions, 60% of the subjects have redundant interactions between the aINS-dlPFC and dlPFC-lOFC about the PPE, and 30% have redundant interactions between lOFC-vmPFC about the RPE. Globally, we reproduced the main results shown in Fig. 3.

Author response image 10.

Inter-subjects reproducibility of redundant interactions about PE signals. Time-courses of proportion of subjects having at least one pair of bipolar derivation with a significant interaction information (p<0.05, cluster-based correction, non-parametric randomization across epochs) about the RPE (blue) or PPE (red). Data are aligned to the outcome presentation (vertical line at 0 seconds). Proportion of subjects with redundant (solid) and synergistic (dashed) interactions are respectively going downward and upward.

Finally, the timings of the observed interactions between areas preclude one of the authors' main conclusions. Specifically, the authors repeatedly concluded that the encoding of RPE/PPE signals are "emerging" from redundancy-dominated prefrontal-insular interactions. However, the between-region information and transfer entropy between vmPFC and lOFC for example is observed almost 500ms after the encoding of RPE/PPE in these regions, questioning how it could possibly lead to the encoding of RPE/PPE. It is also noteworthy that the two information measures, interaction information and transfer entropy, between these areas happened at non overlapping time windows, questioning the underlying mechanism of the communication at play (see Figures 3/4). As an aside, when assessing the direction of information flow, the authors also found delays between pairs of signals peaking at 176ms, far beyond what would be expected for direct communication between nodes. Discussing this aspect might also be of importance as it raises the possibility of third-party involvement.

The local encoding of RPE in the vmPFC and lOFC is observed in a time interval ranging from approximately 0.2-0.4s to 1.2-1.4s after outcome presentation (blue bars in Fig. 2A). The encoding of RPE by interaction information covers a time interval from approximately 1.1s to 1.5s (blue bars in Fig. 3B, bottom right panel). Similarly, significant TE modulations between the vmPFC and lOFC specific for PPE occur mainly in the 0.7s-1.1s range. Thus, it seems that the local encoding of PPE precedes the effects observed at the level of the neural interactions (II and TE). On the other hand, the modulations in MI, II and TE related to PPE co-occur in a time window from 0.2s to 0.7s after outcome presentation. Thus, we agree with the reviewer that a generic conclusion about the potential mechanisms relating the three levels of analysis cannot be drawn. We thus replaced the term “emerge from” by “occur with” from the manuscript which may be misinterpreted as hinting at a potential mechanism. We nevertheless concluded that the three levels of analysis (and phenomena) co-occur in time, thus hinting at a potential across-scales interaction that needs further study. Indeed, our study suggests that further work, beyond the scope of the current study, is required to better understand the interaction between scales.

Regarding the delay for the conditioning of the transfer entropy, the value of 176 ms reflects the delay at which we observed a maximum of transfer entropy. However, we did not use a single delay for conditioning, we used every possible delay between [116, 236] ms, as explained in the Method section. We would like to stress that transfer entropy is a directed metric of functional connectivity, and it can only be interpreted as quantifying statistical causality defined in terms of predictacìbility according to the Wiener-Granger principle, as detailed in the methods. Thus, it cannot be interpreted in Pearl’s causal terms and as indexing any type of direct communication between nodes. This is a known limitation of the method, which has been stressed in past literature and that we believe does not need to be addressed here.

To account for this, we revised the discussion to make sure this issue is addressed in the following paragraph:

“Here, we quantified directional relationships between regions using the transfer entropy (Schreiber, 2000), which is a functional connectivity measure based on the Granger-Wiener causality principle. Tract tracing studies in the macaque have revealed strong interconnections between the lOFC and vmPFC in the macaque (Carmichael and Price, 1996; Öngür and Price, 2000). In humans, cortico-cortical anatomical connections have mainly been investigated using diffusion magnetic resonance imaging (dMRI). Several studies found strong probabilities of structural connectivity between the anterior insula with the orbitofrontal cortex and dorsolateral part of the prefrontal cortex (Cloutman et al., 2012; Ghaziri et al., 2017), and between the lOFC and vmPFC (Heather Hsu et al., 2020). In addition, the statistical dependency (e.g. coherence) between the LFP of distant areas could be potentially explained by direct anatomical connections (Schneider et al., 2021; Vinck et al., 2023). Taken together, the existence of an information transfer might rely on both direct or indirect structural connectivity. However, here we also reported differences of TE between rewarding and punishing trials given the same backbone anatomical connectivity (Fig. 4). [...] “

Reviewer #3:

Summary:

The authors investigated that learning processes relied on distinct reward or punishment outcomes in probabilistic instrumental learning tasks were involved in functional interactions of two different cortico-cortical gamma-band modulations, suggesting that learning signals like reward or punishment prediction errors can be processed by two dominated interactions, such as areas lOFC-vmPFC and areas aINS-dlPFC, and later on integrated together in support of switching conditions between reward and punishment learning. By performing the well-known analyses of mutual information, interaction information, and transfer entropy, the conclusion was accomplished by identifying directional task information flow between redundancy-dominated and synergy-dominated interactions. Also, this integral concept provided a unifying view to explain how functional distributed reward and/or punishment information were segregated and integrated across cortical areas.

Strengths:

The dataset used in this manuscript may come from previously published works (Gueguen et al., 2021) or from the same grant project due to the methods. Previous works have shown strong evidence about why gamma-band activities and those 4 areas are important. For further analyses, the current manuscript moved the ideas forward to examine how reward/punishment information transfer between recorded areas corresponding to the task conditions. The standard measurements such mutual information, interaction information, and transfer entropy showed time-series activities in the millisecond level and allowed us to learn the directional information flow during a certain window. In addition, the diagram in Figure 6 summarized the results and proposed an integral concept with functional heterogeneities in cortical areas. These findings in this manuscript will support the ideas from human fMRI studies and add a new insight to electrophysiological studies with the non-human primates.

We thank the reviewer for the summary such as for highlighting the strengths. Please find below our answers regarding the weaknesses of the manuscript.

Weaknesses:

After reading through the manuscript, the term "non-selective" in the abstract confused me and I did not actually know what it meant and how it fits the conclusion. If I learned the methods correctly, the 4 areas were studied in this manuscript because of their selective responses to the RPE and PPE signals (Figure 2). The redundancy- and synergy-dominated subsystems indicated that two areas shared similar and complementary information, respectively, due to the negative and positive value of interaction information (Page 6). For me, it doesn't mean they are "non-selective", especially in redundancy-dominated subsystem. I may miss something about how you calculate the mutual information or interaction information. Could you elaborate this and explain what the "non-selective" means?

In the study performed by Gueguen et al. in 2021, the authors used a general linear model (GLM) to link the gamma activity to both the reward and punishment prediction errors and they looked for differences between the two conditions. Here, we reproduced this analysis except that we used measures from the information theory (mutual information) that were able to capture linear and non-linear relationships (although monotonic) between the gamma activity and the prediction errors. The clusters we reported reflect significant encoding of either the RPE and/or the PPE. From Fig. 2, it can be seen that the four regions have a gamma activity that is modulated according to both reward and punishment PE. We used the term “non-selective”, because the regions did not encode either one or the other, but various proportions of bipolar derivations encoding either one or both of them.

The directional information flows identified in this manuscript were evidenced by the recording contacts of iEEG with levels of concurrent neural activities to the task conditions. However, are the conclusions well supported by the anatomical connections? Is it possible that the information was transferred to the target via another area? These questions may remain to be elucidated by using other approaches or animal models. It would be great to point this out here for further investigation.

We thank the reviewer for this interesting question. We added the following paragraph to the discussion to clarify the current limitations of the transfer entropy and the link with anatomical connections :

“Here, we quantified directional relationships between regions using the transfer entropy (Schreiber, 2000), which is a functional connectivity measure based on the Granger-Wiener causality principle. Tract tracing studies in the macaque have revealed strong interconnections between the lOFC and vmPFC in the macaque (Carmichael and Price, 1996; Öngür and Price, 2000). In humans, cortico-cortical anatomical connections have mainly been investigated using diffusion magnetic resonance imaging (dMRI). Several studies found strong probabilities of structural connectivity between the anterior insula with the orbitofrontal cortex and dorsolateral part of the prefrontal cortex (Cloutman et al., 2012; Ghaziri et al., 2017), and between the lOFC and vmPFC (Heather Hsu et al., 2020). In addition, the statistical dependency (e.g. coherence) between the LFP of distant areas could be potentially explained by direct anatomical connections (Schneider et al., 2021). Taken together, the existence of an information transfer might rely on both direct or indirect structural connectivity. However, here we also reported differences of TE between rewarding and punishing trials given the same backbone anatomical connectivity (Fig. 4). Our results are further supported by a recent study involving drug-resistant epileptic patients with resected insula who showed poorer performance than healthy controls in case of risky loss compared to risky gains (Von Siebenthal et al., 2017).”

References

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Cloutman LL, Binney RJ, Drakesmith M, Parker GJM, Lambon Ralph MA. 2012. The variation of function across the human insula mirrors its patterns of structural connectivity: Evidence from in vivo probabilistic tractography. NeuroImage 59:3514–3521. oi:10.1016/j.neuroimage.2011.11.016

Combrisson E, Allegra M, Basanisi R, Ince RAA, Giordano BL, Bastin J, Brovelli A. 2022. Group-level inference of information-based measures for the analyses of cognitive brain networks from neurophysiological data. NeuroImage 258:119347. doi:10.1016/j.neuroimage.2022.119347

Ghaziri J, Tucholka A, Girard G, Houde J-C, Boucher O, Gilbert G, Descoteaux M, Lippé S, Rainville P, Nguyen DK. 2017. The Corticocortical Structural Connectivity of the Human Insula. Cereb Cortex 27:1216–1228. doi:10.1093/cercor/bhv308

Gueguen MCM, Lopez-Persem A, Billeke P, Lachaux J-P, Rheims S, Kahane P, Minotti L, David O, Pessiglione M, Bastin J. 2021. Anatomical dissociation of intracerebral signals for reward and punishment prediction errors in humans. Nat Commun 12:3344. doi:10.1038/s41467-021-23704-w

Heather Hsu C-C, Rolls ET, Huang C-C, Chong ST, Zac Lo C-Y, Feng J, Lin C-P. 2020. Connections of the Human Orbitofrontal Cortex and Inferior Frontal Gyrus. Cereb Cortex 30:5830–5843. doi:10.1093/cercor/bhaa160

Lachaux J-P, Fonlupt P, Kahane P, Minotti L, Hoffmann D, Bertrand O, Baciu M. 2007. Relationship between task-related gamma oscillations and BOLD signal: new insights from combined fMRI and intracranial EEG. Hum Brain Mapp 28:1368–1375. doi:10.1002/hbm.20352

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Öngür D, Price JL. 2000. The organization of networks within the orbital and medial prefrontal cortex of rats, monkeys and humans. Cereb Cortex 10:206–219.

Schneider M, Broggini AC, Dann B, Tzanou A, Uran C, Sheshadri S, Scherberger H, Vinck M. 2021. A mechanism for inter-areal coherence through communication based on connectivity and oscillatory power. Neuron 109:4050-4067.e12. doi:10.1016/j.neuron.2021.09.037

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Von Siebenthal Z, Boucher O, Rouleau I, Lassonde M, Lepore F, Nguyen DK. 2017. Decision-making impairments following insular and medial temporal lobe resection for drug-resistant epilepsy. Soc Cogn Affect Neurosci 12:128–137. doi:10.1093/scan/nsw152

Recommendations for the authors

Reviewer #1

(1) Overall, the writing of the manuscript is dense and makes it hard to follow the scientific logic and appreciate the key findings of the manuscript. I believe the manuscript would be accessible to a broader audience if the authors improved the writing and provided greater detail for their scientific questions, choice of analysis, and an explanation of their results in simpler terms.

We extensively modified the introduction to better describe the rationale and research question.

(2) In the introduction the authors state "we hypothesized that reward and punishment learning arise from complementary neural interactions between frontal cortex regions". This stated hypothesis arrives rather abruptly after a summary of the literature given that the literature summary does not directly inform their stated hypothesis. Put differently, the authors should explicitly state what the contradictions and/or gaps in the literature are, and what specific combinations of findings guide them to their hypothesis. When the authors state their hypothesis the reader is still left asking: why are the authors focusing on the frontal regions? What do the authors mean by complementary interactions? What specific evidence or contradiction in the literature led them to hypothesize that complementary interactions between frontal regions underlie reward and punishment learning?

We extensively modified the introduction and provided a clearer description of the brain circuits involved and the rationale for searching redundant and synergistic interactions between areas.

(3) Related to the above point: when the authors subsequently state "we tested whether redundancy- or synergy dominated interactions allow the emergence of collective brain networks differentially supporting reward and punishment learning", the Introduction (up to the point of this sentence) has not been written to explain the synergy vs. redundancy framework in the literature and how this framework comes into play to inform the authors' hypothesis on reward and punishment learning.

We extensively modified the introduction and provided a clearer description of redundant and synergistic interactions between areas.

(4) The explanation of redundancy vs synergy dominated brain networks itself is written densely and hard to follow. Furthermore, how this framework informs the question on the neural substrates of reward versus punishment learning is unclear. The authors should provide more precise statements on how and why redundancy vs. synergy comes into play in reward and punishment learning. Put differently, this redundancy vs. synergy framework is key for understanding the manuscript and the introduction is not written clearly enough to explain the framework and how it informs the authors' hypothesis and research questions on the neural substrates of reward vs. punishment learning.

Same as above

(5) While the choice of these four brain regions in context of reward and punishment learning does makes sense, the authors do not outline a clear scientific justification as to why these regions were selected in relation to their question.

Same as above

(6) Could the authors explain why they used gamma band power (as opposed to or in addition to the lower frequency bands) to investigate MI. Relatedly, when the authors introduce MI analysis, it would be helpful to briefly explain what this analysis measures and why it is relevant to address the question they are asking.

Please see our answer to the first public comment. We added a paragraph to the discussion section to justify our choice of focusing on the gamma band only. We added the following sentence to the result section to justify our choice for using mutual-information:

The MI allowed us to detect both linear and non-linear relationships between the gamma activity and the PE

An extended explanation justifying our choice for the MI was already present in the method section.

(7) The authors state that "all regions displayed a local "probabilistic" encoding of prediction errors with temporal dynamics peaking around 500 ms after outcome presentation". It would be helpful for the reader if the authors spelled out what they mean by probabilistic in this context as the term can be interpreted in many different ways.

We agree with the reviewer that the term “probabilistic” can be interpreted in different ways. In the revised manuscript we changed “probabilistic” for “mixed”.

(8) The authors should include a brief description of how they compute RPE and PPE in the beginning of the relevant results section.

The explanation of how we estimated the PE is already present in the result section: “We estimated trial-wise prediction errors by fitting a Q-learning model to behavioral data. Fitting the model consisted in adjusting the constant parameters to maximize the likelihood of observed choices etc.”

(9) It is unclear from the Methods whether the authors have taken any measures to address the likely difference in the number of electrodes across subjects. For example, it is likely that some subjects have 10 electrodes in vmPFC while others may have 20. In group analyses, if the data is simply averaged across all electrodes then each subject contributes a different number of data points to the analysis. Hence, a subject with more electrodes can bias the group average. A starting point would be to state the variation in number of electrodes across subjects per brain region. If this variation is rather small, then simple averaging across electrodes might be justified. If the variation is large then one idea would be to average data across electrodes within subjects prior to taking the group average or use a resampling approach where the minimum number of electrodes per brain area is subsampled.

We addressed this point in our public answers. As a reminder, the new version of the manuscript contains a figure showing the number of unique patients per region, the PE at per participant level together with local-encoding at the single participant level.

(10) One thing to consider is whether the reward and punishment in the task is symmetrical in valence. While 1$ increase and 1$ decrease is equivalent in magnitude, the psychological effect of the positive (vs. the negative) outcome may still be asymmetrical and the direction and magnitude of this asymmetry can vary across individuals. For instance, some subjects may be more sensitive to the reward (over punishment) while others are more sensitive to the punishment (over reward). In this scenario, it is possible that the differentiation observed in PPE versus RPE signals may arise from such psychological asymmetry rather than the intrinsic differences in how certain brain regions (and their interactions) may encode for reward vs punishment. Perhaps the authors can comment on this possibility, and/or conduct more in depth behavioral analysis to determine if certain subjects adjust their choice behavior faster in response to reward vs. punishment contexts.

While it could be possible that individuals display different sensitivities vis-à-vis positive and negative prediction errors (and, indeed, a vast body of human reinforcement learning literature seems to point in this direction; Palminteri & Lebreton, 2022), it is unclear to us how such differences would explain into the recruitment of anatomically distinct areas reward and punishment prediction errors. It is important to note here that our design partially orthogonalized positive and reward vs. negative and punishment PEs, because the neutral outcome can generate both positive and negative prediction errors, as a function of the learning context (reward-seeking and punishment avoidance). Back to the main question, for instance, Lefebvre et al (2017) investigated with fMRI the neural correlates of reward prediction errors only and found that inter-individual differences in learning rates for positive and negative prediction errors correlated with differences in the degree of striatal activation and not with the recruitment of different areas. To sum up, while we acknowledge that individuals may display different sensitivity to prediction errors (and reward magnitudes), we believe that such differences should translated in difference in the degree of activation of a given system (the reward systems vs the punishment one) rather than difference in neural system recruitment

(11) As summarized in Fig 6, the authors show that information transfer between aINS to dlPFC was PPE specific whereas the information transfer between vmPFC to lOFC was RPE specific. What is unclear is if these findings arise as an inevitable statistical byproduct of the fact that aINS has high PPE-specificity and that vmPFC has high RPE-specificity. In other words, it is possible that the analysis in Fig 3,4 are sensitive to fact that there is a larger proportion of electrodes with either PPE or RPE sensitivity in aINS and vmPFC respectively - and as such, the II analysis might reflect the dominant local encoding properties above and beyond reflecting the interactions between regions per se. Simply put, could the analysis in Fig 3B turn out in any other way given that there are more PPE specific electrodes in aINS and more RPE specific electrodes in vmPFC? Some options to address this question would be to limit the electrodes included in the analyses (in Fig 3B for example) so that each region has the same number of PPE and RPE specific electrodes included.

Please see the simulation we added to the revised manuscript (Fig. S10) demonstrating that synergistic interactions can emerge between regions with the same specificity.

Regarding the possibility that Fig. 3 and 4 are sensitive to the number of bipolar derivations being R/PPE specific, a counter-example is the vmPFC. The vmPFC has a few recordings specific to punishment (Fig. 2) in almost 30% of the subjects (Fig. S4). However, there is no II about the PPE between recordings of the vmPFC (Fig. 3). The same reasoning also holds for the lOFC. Therefore, the proportion of recordings being RPE or PPE-specific is not sufficient to determine the type of interactions.

(12)  Related to the point above, what would the results presented in Fig 3A (and 3B) look like if the authors ran the analyses on RPE specific and PPE specific electrodes only. Is the vmPFC-vmPFC RPE effect in Fig 3A arising simply due to the high prevalence of RPE specific electrodes in vmPFC (as shown in Fig. 2)?

Please see our answer above.

Reviewer #2:

Regarding Figure 2A, the authors argued that their findings "globally reproduced their previously published findings" (from Gueguen et al, 2021). It is worth noting though that in their original analysis, both aINS and lOFC show differential effects (aINS showing greater punishment compared to reward, and the opposite for lOFC) compared to the current analysis. Although I would be akin to believe that the nonlinear approach used here might explain part of the differences (as the authors discussed), I am very wary of the other argument advanced: "the removal of iEEG sites contaminated with pathological activity". This raised some red flags. Does that mean some of the conclusions observed in Gueguen et al (2021) are only the result of noise contamination, and therefore should be disregarded? The author might want to add a short supplementary figure using the same approach as in Gueguen (2021) but using the subset of contacts used here to comfort potential readers of the validity of their previous manuscript.

We appreciate the reviewer's concerns and understand the request for additional information. However, we would like to point out that the figure suggested by the reviewer is already present in the supplementary files of Gueguen et al. 2021 (see Fig. S2). The results of this study should not be disregarded, as the supplementary figure reproduces the results of the main text after excluding sites with pathological activity. Including or excluding sites contaminated with epileptic activity does not have a significant impact on the results, as analyses are performed at each time-stamp and across trials, and epileptic spikes are never aligned in time across trials.

That being said, there are some methodological differences between the two studies. To extract gamma power, Gueguen et al. filtered and averaged 10 Hz sub-bands, while we used multi-tapers. Additionally, they used a temporal smoothing of 250 ms, while we used less smoothing. However, as explained in the main text, we used information-theoretical approaches to capture the statistical dependencies between gamma power and PE. Despite divergent methodologies, we obtained almost identical results.

The data and code supporting this manuscript should be made available. If raw data cannot be shared for ethical reasons, single-trial gamma activities should at least be provided. Regarding the code used to process the data, sharing it could increase the appeal (and use) of the methods applied.

We thank the reviewer for this suggestion. We added a section entitled “Code and data availability” and gave links to the scripts, notebooks and preprocessed data.

Author Response:

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

eLife assessment

This study presents potentially useful findings describing how activity in the corticotropin-releasing hormone neurons in the paraventricular nucleus of the hypothalamus modulates sevoflurane anesthesia, as well as a phenomenon the authors term a "general anesthetic stress response". The technical approaches are solid and the data presented are largely clear. However, the primary conclusion, that the PVHCRH neurons are a mechanism of sevoflurane anesthesia, is inadequately supported.

We appreciate the editors and reviewers for their thorough assessment and constructive feedback. We have provided clarifications and updated the manuscripts to better interpret our results, please see below. As for the primary conclusion, we revised it as PVH CRH neurons potently modulate states of anaesthesia in sevoflurane general anesthesia, being a part of anaesthesia regulatory network of sevoflurane.

Combined Public Review:

This study describes a group of CRH-releasing neurons, located in the paraventricular nucleus of the hypothalamus, which, in mice, affects both the state of sevoflurane anesthesia and a grooming behavior observed after it. PVH-CRH neurons showed elevated calcium activity during the post-anesthesia period. Optogenetic activation of these PVH-CRH neurons during sevoflurane anesthesia shifts the EEG from burst-suppression to a seemingly activated state (an apparent arousal effect), although without a behavioral correlate. Chemogenetic activation of the PVH-CRH neurons delays sevoflurane-induced loss of righting reflex (another apparent arousal effect). On the other hand, chemogenetic inhibition of PVH-CRH neurons delays recovery of the righting reflex and decreases sevoflurane-induced stress (an apparent decrease in the arousal effect). The authors conclude that PVH-CRH neurons are a common substrate for sevoflurane-induced anesthesia and stress. The PVH-CRH neurons are related to behavioral stress responses, and the authors claim that these findings provide direct evidence for a relationship between sevoflurane anesthesia and sevoflurane-mediated stress that might exist even when there is no surgical trauma, such as an incision. In its current form, the article does not achieve its intended goal.

Thank you for the detailed review. We have carefully considered your comments and have revised the manuscript to provide a clearer interpretation of our findings. Our findings indicate that PVH CRH neurons integrate the anesthetic effect and post-anesthesia stress response of sevoflurane (GA), providing new evidence for understanding the neuronal regulation of sevoflurane GA and identifying a potential brain target for further investigation into modulating the post-anesthesia stress response. However, we did not propose that there was a direct relationship between sevoflurane anesthesia and sevoflurane-mediated stress in the absence of incision. Our results mainly concluded that PVH CRH neurons integrate the anaesthetic effect and post-anaesthesia stress response of sevoflurane GA, which offers new evidence for the neuronal regulation of sevoflurane GA and provides an important but ignored potential cause of the post-anesthesia stress response.

Strengths:

The manuscript uses targeted manipulation of the PVH-CRH neurons, and is technically sound. Also, the number of experiments is substantial.

Thank you.

Weaknesses:

The most significant weaknesses are a) the lack of consideration and measurement of GABAergic mechanisms of sevoflurane anesthesia, b) the failure to use another anesthetic as a control, c) a failure to document a compelling post-anesthesia stress response to sevoflurane in humans, d) limitations in the novelty of the findings. These weaknesses are related to the primary concerns described below:

Concerns about the primary conclusion, that PVH-CRH neurons mediate "the anesthetic effects and post-anesthesia stress response of sevoflurane GA".

Thanks for the advice. Our responses are as below:

1) Just because the activity of a given neural cell type or neural circuit alters an anesthetic's response, this does not mean that those neurons play a role in how the anesthetic creates its anesthetic state. For example, sevoflurane is commonly used in children. Its primary mechanism of action is through enhancement of GABA-mediated inhibition. Children with ADHD on Ritalin (a dopamine reuptake inhibitor) who take it on the day of surgery can often require increased doses of sevoflurane to achieve the appropriate anesthetic state. The mesocortical pathway through which Ritalin acts is not part of the mechanism of action of sevoflurane. Through this pathway, Ritalin is simply increasing cortical excitability making it more challenging for the inhibitory effects of sevoflurane at GABAergic synapses to be effective. Similarly, here, altering the activity of the PVHCRH neurons and seeing a change in anesthetic response to sevoflurane does not mean that these neurons play a role in the fundamental mechanism of this anesthetic's action. With the current data set, the primary conclusions should be tempered.

Thank you for your comments. Our results adequately uncover PVH CRH neurons that modulate the state of consciousness as well as the stress response in sevoflurane GA, but are insufficient to demonstrate that these neurons play a role in the underlying mechanism of sevoflurane anesthesia. We will revise our conclusions and make them concrete. The primary conclusion has been revised as PVH CRH neurons potently modulate states of anaesthesia in sevoflurane GA, being a part of the anaesthesia regulatory network of sevoflurane.

2) It is important to compare the effects of sevoflurane with at least one other inhaled ether anesthetic. Isoflurane, desflurane, and enflurane are ether anesthetics that are very similar to each other, as well as being similar to sevoflurane. It is important to distinguish whether the effects of sevoflurane pertain to other anesthetics, or, alternatively, relate to unique idiosyncratic properties of this gas that may not be a part of its anesthetic properties.

For example, one study cited by the authors (Marana et al.. 2013) concludes that there is weak evidence for differences in stress-related hormones between sevoflurane and desflurane, with lower levels of cortisol and ACTH observed during the desflurane intraoperative period. It is not clear that this difference in some stress-related hormones is modeled by post-sevoflurane excess grooming in the mice, but using desflurane as a control could help determine this.

Thank you for your suggestions. We completely agree on the importance of determining whether the effects of sevoflurane apply to other anesthetics or arise from unique idiosyncratic attributes separate from its anesthetic properties. However, it is challenging to definitively conclude whether the effects of sevoflurane observed in our study extend to other inhaled anesthetics, even with desflurane as a control. While sevoflurane shares many common anesthetic properties with other inhalation agents, it also exhibits distinct characteristics and potential idiosyncrasies that set it apart from its counterparts. Regarding studies related to desflurane's impact on hormone levels or stress-like behaviors, one study involving 20 women scheduled for elective total abdominal hysterectomy demonstrated that there was no significant correlation between the intra-operative depth of anesthesia achieved with desflurane and the extent of the endocrine-metabolic stress response (as indicated by the concentrations of plasma cortisol, glucose, and lactate)1. Besides, a study conducted with mice suggested the abilities related to sensorimotor functions, anxiety and depression did not undergo significant changes after 7 days of anesthesia administered with 8.0% desflurane for 6 h2. Furthermore, a study involving 50 Caucasian women undergoing laparoscopic surgery for benign ovarian cysts demonstrated that in low stress surgery, desflurane, when compared to sevoflurane, exhibited superior control over the intraoperative cortisol and ACTH response 3. Based on these findings, we propose that the effect we observed in this study is likely attributed to the unique idiosyncratic properties of sevoflurane. We will conduct additional experiments to investigate this proposal with other commonly used anaesthetics in our future studies.

Concerns about the clinical relevance of the experiments

In anesthesiology practice, perioperative stress observed in patients is more commonly related to the trauma of the surgical intervention, with inadequate levels of antinociception or unconsciousness intraoperatively and/or poor post-operative pain control. The authors seem to be suggesting that the anesthetic itself is causing stress, but there is no evidence of this from human patients cited. We were not aware that this is a documented clinical phenomenon. It is important to know whether sevoflurane effectively produces behavioral stress in the recovery room in patients that could be related to the putative stress response (excess grooming) observed in mice. For example, in surgeries or procedures that required only a brief period of unconsciousness that could be achieved by administering sevoflurane alone (comparable to the 30 min administered to the mice), is there clinical evidence of post-operative stress?

Thank you for your question. There is currently no direct evidence available. Studies on sevoflurane in humans primarily focus on its use during surgical interventions, making it difficult to find studies that solely administer sevoflurane, as was done in our study with mice. Generally, a short anesthesia time refers to procedures that last less than one hour, while a long anesthesia time could be considered for procedures lasting several hours or more4. A study published in eLife investigated the patterns of reemerging consciousness and cognitive function in 30 healthy adults who underwent GA for three hours 5. This finding suggests that the cognitive dysfunction observed immediately and persistently after GA in healthy animals may not necessarily apply anesthesia and postoperative neurocognitive disorders could be influenced by factors other than GA, such as surgery or patient comorbidity. Therefore, further studies are needed to verify the post-operative stress in sevoflurane-only short time anesthesia.

Indeed, stress after surgeries can result from multiple factors aside from anesthesia, including pain, anxiety, inflammation, but what we want to illustrate in this study is that anesthesia could be one of these factors that we ignored in previous studies. In our current study, we did not propose that there was a direct relationship between sevoflurane anesthesia and sevoflurane-mediated stress without incision. We observed stress-related behavioural changes after exposure of sevoflurane GA in mouse model, indicating sevoflurane-mediated stress might exist without surgical trauma. Importantly, whether anesthetic administration alone will cause post-operative stress is worth studying in different species especially human.

Patients who receive sevoflurane as the primary anesthetic do not wake up more stressed than if they had had one of the other GABAergic anesthetics. If there were signs of stress upon emergence (increased heart rate, blood pressure, thrashing movements) from general anesthesia, the anesthesiologist would treat this right away. The most likely cause of post-operative stress behaviors in humans is probably inadequate anti-nociception during the procedure, which translates into inadequate post-op analgesia and likely delirium. It is the case that children receiving sevoflurane do have a higher likelihood of post-operative delirium. Perhaps the authors' studies address a mechanism for delirium associated with sevoflurane, but this is not considered. Delirium seems likely to be the closest clinical phenomenon to what was studied.

We agree with your idea. We aim to establish a connection between post-operative delirium in humans and stress-like behaviors observed in mice following sevoflurane anesthesia. Specifically, we have observed that the increased grooming behavior exhibited by mice after sevoflurane anesthesia resembles the fuzzy state of consciousness experienced during post-operative delirium6. In our discussion, we also emphasized the occurrence of sevoflurane-induced emergence agitation, a common phenomenon reported in clinical studies with an incidence of up to 80%. This state is characterized by hyperactivity, confusion, delirium, and emotional agitation 7,8. Meanwhile, in our experimental tests, namely the open field test (OFT) and elevated plus maze (EPM) test, we observed that mice exposed to sevoflurane inhalation displayed reduced movement distances during both the OFT and EPM tests (Figure 7G and I). These findings suggest a decline in behavioral activity similar to what is observed in cases of delirium.

Concerns about the novelty of the findings

CRH is associated with arousal in numerous studies. In fact, the authors' own work, published in eLife in 2021, showed that stimulating the hypothalamic CRH cells leads to arousal and their inhibition promotes hypersomnia. In both papers, the authors use fos expression in CRH cells during a specific event to implicate the cells, then manipulate them and measure EEG responses. In the previous work, the cells were active during wakefulness; here- they were active in the awake state that follows anesthesia (Figure 1). Thus, the findings in the current work are incremental.

Thank you for acknowledging our previous work focusing on the changes in the sleep-wake state of mice when PVH CRH neurons are manipulated. In this study, our primary objective was to identify the neuronal mechanisms mediating the anesthetic effects and post-anesthetic stress response of sevoflurane GA. While our study claims that activation of PVH CRH neurons leads to arousal, it provides evidence that PVH CRH neurons may play a role in the regulation of conscious states in GA. Our current findings uncover that PVH CRH neurons modulate the state of consciousness as well as the stress response in sevoflurane GA, and that the modulation of PVH CRH neurons bidirectionally altered the induction and recovery of sevoflurane GA. This identifies a new brain region involved in sevoflurane GA that goes beyond the arousal-related regions.

The activation of CRH cells in PVN has already been shown to result in grooming by Jaideep Bains (cited as reference 58). Thus, the involvement of these cells in this behavior is expected. The authors perform elaborate manipulations of CRH cells and numerous analyses of grooming and related behaviors. For example, they compare grooming and paw licking after anesthesia with those after other stressors such as forced swim, spraying mice with water, physical attack, and restraint. However, the relevance of these behaviors to humans and generalization to other types of anesthetics is not clear.

The hyperactivity of PVH CRH neurons and behavior (e.g., excessive self-grooming) in mice may partially mirror the observed agitation and underlying mechanisms during emergence from sevoflurane GA in patients. As mentioned in the Discussion section (page 16, lines 371-374), sevoflurane-induced emergence agitation represents a prevalent manifestation of the post-anesthesia stress response. It is frequently observed, with an incidence of up to 80% in clinical reports, and is characterized by hyperactivity, confusion, delirium, and emotional agitation7,8. Our aim in this study is to distinguish the excessive stress responses of patients to sevoflurane GA from stress triggered by other factors. Other stimuli, such as forced swimming, can be considered sources of both physical and emotional stress, which are associated with depression and anxiety in humans.

Regarding generalization to other types of anesthetics, we propose that the stress-related behavioral effects observed in this study might occur in cases of the administration of certain types of anesthetics. For example, one study showed that intravenous ketamine infusion (10 mg/kg, 2 hours) elevated plasma corticosterone and progesterone levels in rats, reducing locomotor activity (sedation) 9. The administration of intravenous anesthesia with propofol combined with sevoflurane caused greater postoperative stress than the single use of propofol10. However, desflurane, a common inhaled ether anesthetic, when compared to sevoflurane, was associated with better control of intraoperative cortisol and ACTH response in low-stress surgeries8. Thus, these behaviors observed after exposure to sevoflurane GA may be related to the post-anesthesia stress response in humans, which might also occur in cases of the administration of certain types of anesthetics.

Recommendations for the authors:

Reviewer 1

1) The CRH-Cre mouse line should be validated. There are several lines of these mice, and their fidelity varies.

The CRH-Cre mouse line we used in this study is from The Jackson Laboratory (https://www.jax.org/strain/012704) with the name B6(Cg)-Crhtm1(cre)Zjh/J (Strain #: 012704). These CRH-ires-CRE knock-in mice have Cre recombinase expression directed to CRH positive neurons by the endogenous promoter/enhancer elements of the corticotropin releasing hormone locus (Crh). We have done standard PCR to validate the mouse line following genotyping protocols provided by the Jackson Laboratory. The protocol primers were: 10574 (SEQUENCE 5' → 3': CTT ACA CAT TTC GTC CTA GCC); 10575 (SEQUENCE 5' → 3': CAC GAC CAG GCT GCG GCT AAC); 10576 (SEQUENCE 5' → 3': CAA TGT ATC TTA TCA TGT CTG GAT CC). The 468-bp CRH-specific PCR product was amplified in mutant (CRH-Cre+/+) mice; in heterozygote (CRH-Cre+/-) mice, both the 468-bp and the 676-bp PCR products were detected; in wild type (WT) mice, only the 676-bp WT allele-specific PCR product was amplified. An example of PCR results is presented below. The heterozygote and mutant mice were included in our study.

Author response image 1.

1. It would be very helpful to validate the CRH antibody. Using any antiserum at 1:800 suggests that it may not be potent or highly specific.

As requested, we used the same CRH antibody at a concentration of 1:800, following the methods described in the Method section. The results are displayed below.

Author response image 2.

1. In Figure 1C, the control sections are out of focus, any cells are blurry, reducing confidence in the analyses (locus ceruleus cells appear confluent in the control?)

Sorry for the confusing figure and we have revised the control section part of Figure 1C:

Author response image 3.

Reviewer 2

1) In the Abstract, to say that "General anesthetics benefit patients undergoing surgeries without consciousness. ..." is a gross understatement of the essential role that general anesthesia plays today to make surgery not only tolerable but humane. This opening sentence should be rewritten. General anesthesia is a fundamental process required to undertake safely and humanely a high fraction of surgeries and invasive diagnostic procedures.

As requested, we rewrote this opening sentence, please see the follows:

GA is a fundamental process required to undertake surgeries and invasive diagnostic procedures safely and humanely. However, the undesired stress response associated with GA can lead to delayed recovery and even increased morbidity in clinical settings.

2) In the Abstract, when discussing the response of the PVN-CRH neurons to chemogenetic inhibition, say exactly what the "opposite effect" is.

Thanks for your insights. We have rewritten our abstract as follows:

Chemogenetic activation of these neurons delayed the induction and accelerated emergence from sevoflurane GA, whereas chemogenetic inhibition of PVH CRH neurons promoted induction and prolonged emergence from sevoflurane GA.

3) In all spectrograms the dynamic range is compressed between 0.5 and 1. Please make use of the full range, as some details might be missed because of this compression.

We are sorry for the incorrect unit of the spectrograms. We have provided the correct one with full range, please see below:

Author response image 4.

Author response image 5.

4) The spectrogram in Figure 2D has several frequency chirps that do not seem physiological.

Thank you for your comments. The frequency chips of the spectrogram during the During and Post 1 phase were caused by recording noises. To avoid confusion, we have deleted the spectrogram in Figure 2D.

5) The 3D plots in Figures 3G and H are not helpful. Thanks for the comment. We'd like to keep the 3D plots as they aid visual comparison of three different features of grooming, which complements other panels in Figure 3.

6) The spectrograms in Figures 5A and B are too small, while the spectra in Figures 5C and D are too large. Please invert this relationship, as it is interesting and important to see the details in the spectrograms. The same happens in Figure 6.

We adjusted the layout of the Figure 5 and Figure 6 as requested, please see below:

Author response image 6.

Author response image 7.

7) In Figure 6H, the authors compute the burst-suppression ratio during a period that seemingly has no bursts or suppressions (Figure 6B).

The burst-suppression ratio was computed from data with the minimum duration of burst and suppression periods set at 0.5 s. Sorry for the confusion. We added a new supplementary figure (Figure 6-figure supplement 8) displaying a 40-second EEG with a burst suppression period to better visualize the burst suppression.

Author response image 8.

8) The data analyses are done in terms of p-values. They should be reported as confidence intervals so that any effect the authors wish to establish is measured along with its uncertainty.

Thank you for your valuable suggestions regarding our manuscript. We appreciate your thoughtful consideration of our work. We understand your concern but we would like to provide some justification for our choice of reporting p-values and explain why we believe they are appropriate for our study. First, the use of p-values for hypothesis testing and significance assessment is a common practice in our field. Many previous studies in our area of research also report results in terms of p-values. For example, Wei Xu11 published in 2020 suggested sevoflurane inhibits MPB neurons through postsynaptic GABAA-Rs and background potassium channels, Ao Y12 demonstrated that activation of the TH:LC-PVT projections is helpful in facilitating the transition from isoflurane anesthesia to an arousal state, using P-value as data analyses. By adhering to this convention, we ensure that our findings are consistent with the existing body of literature. This makes it easier for readers to compare and integrate our results with previous work. Secondly, while confidence intervals can provide a measure of effect size and uncertainty, p-values offer a concise way to communicate statistical significance. They help readers quickly assess whether an effect is statistically significant or not, which is often the primary concern when interpreting research findings. We hope that by providing these reasons for our choice of reporting p-values, we can address your concern while maintaining the integrity and consistency of our study. If you believe there are specific instances where reporting confidence intervals would be more informative, please feel free to highlight those, and we will consider your suggestion on a case-by-case basis. 

References

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