Author response:

The following is the authors’ response to the original reviews

Reviewer #1:

The authors sought to examine the associations between child age, reports of parent-child relationship quality, and neural activity patterns while children (and also their parents) watched a movie clip. Major methodological strengths include the sample of 3-8 year-old children in China (rare in fMRI research for both age range and non-Western samples), use of a movie clip previously demonstrated to capture theory of mind constructs at the neural level, measurement of caregiver-child neural synchrony, and assessment of neural maturity. Results provide important new information about parent-child neural synchronization during this movie and associations with reports of parent-child relationship quality. The work is a notable advance in understanding the link between the caregiving context and the neural construction of theory of mind networks in the developing brain.

We are grateful for the reviewer’s generous and thoughtful summary of our work. We particularly appreciate the recognition of the methodological strengths—including the rare developmental sample, culturally diverse context, and use of naturalistic, theory of mind-relevant stimuli—as well as the importance of integrating neural synchrony and relational variables. The reviewer’s comments affirm the core motivation behind this study: to advance our understanding of how the caregiving environment shapes the neurodevelopment of social cognition in early childhood. We have taken all specific suggestions seriously and hope the revised manuscript more clearly communicates these contributions.

We appreciate that the authors wanted to show support for a mediational mechanism. However, we suggest that the authors drop the structural equation modeling because the data are cross-sectional so mediation is not appropriate. Other issues include the weak justification of including the parent-child neural synchronization as part of parenting.... it could just as easily be a mechanism of change or driven by the child rather than a component of parenting behavior. The paper would be strengthened by looking at associations between selected variables of interest that are MOST relevant to the imaging task in a regression type of model. Furthermore, the authors need to be more explicit about corrections for multiple comparisons throughout the manuscript; some of the associations are fairly weak so claims may need to be tempered if they don't survive correction.

Thanks for feedback on the use of SEM in our study. We recognize the limitations of using SEM to infer mediation with cross-sectional data and acknowledge that longitudinal designs are better suited for such analyses. However, our goal was not to establish causality but to explore potential pathways linking parenting, personal traits, and Theory of Mind (ToM) behavior to social cognition outcomes. SEM allowed us to simultaneously examine the relationships among these latent constructs, providing a cohesive framework for understanding the interplay of these factors. That said, we understand your concern and are willing to revise the manuscript to de-emphasize causal interpretations of the SEM findings.

We thank the reviewer for raising the corrections for multiple comparisons. We confirm that all correlation analyses reported in the manuscript have been corrected for multiple comparisons using the False Discovery Rate (FDR) procedure. In the revised manuscript, we now explicitly indicate FDR correction for all relevant p-values to ensure clarity and transparency. Where this information was previously missing, we have corrected the oversight and clearly labeled the results as FDR-corrected or uncorrected where appropriate. Additionally, we have carefully reviewed our interpretation of all reported associations. For any results that were close to the significance threshold, we have tempered our claims and now describe them as a marginally significant association to avoid overstating our findings.

The corresponding changes have been made on Discussion section of the revised manuscript.

Reverse correlation analysis is sensible given what prior developmental fMRI studies have done. But reverse correlation analysis may be more prone to overfitting and noise, and lacks sensitivity to multivariate patterns. Might inter-subject correlation be useful for *within* the child group? This would minimize noise and allow for non-linear patterns to emerge.

We appreciate the reviewer’s thoughtful suggestion regarding potential limitations of reverse correlation analysis. While we agree that inter-subject correlation (ISC) within the child group may be useful in other contexts, our primary goal in using reverse correlation was not to identify temporally distributed or multivariate response patterns, but rather to isolate specific events within the naturalistic stimulus that reliably evoke Theory of Mind (ToM) and Social Pain-related responses in adults—who possess more stable and mature neural signatures. These adult-derived events serve as anchors for subsequent developmental comparisons and provide a principled way to define timepoints of interest that are behaviorally and theoretically meaningful.

Using reverse correlation in adults allows us to identify canonical ToM and Social Pain events in a data-driven yet hypothesis-informed manner. We then examine how children’s neural responses to these same events vary with age, neural maturity, and dyadic synchrony. This approach is consistent with prior work in developmental social neuroscience (e.g., Richardson et al., 2018) and offers a valid framework for identifying interpretable social-cognitive events in naturalistic stimuli.

We have now clarified the rationale for using adult-based reverse correlation in the revised manuscript and explicitly stated its advantages for identifying targeted ToM and Social Pain content in the stimulus.

The corresponding changes have been made on pages 17 of the revised manuscript.

“We employed reverse correlation analysis in adults to identify discrete events within the movie that elicited reliable neural responses across participants in ToM and SPM networks.

The events of adults were chosen for this analysis due to the relative stability and maturity of their social brain responses, allowing for robust detection of canonical ToM and social pain-related moments. These events, once identified, served as stimulus-locked timepoints for subsequent analyses in the child cohort. This approach enables us to examine how children's responses to well-characterized, socially meaningful events vary with age and parent-child dyadic dynamics.”

No learning effects or temporal lagged effects are tested in the current study, so the results do not support the authors' conclusions that the data speak to Bandura's social learning theory. The authors do mention theories of biobehavioral synchrony in the introduction but do not discuss this framework in the discussion (which is most directly relevant to the data). The data can also speak to other neurodevelopmental theories of development (e.g.,neuroconstructivist approaches), but the authors do not discuss them. The manuscript would benefit from significantly revising the framework to focus more on biobehavioral synchrony data and other neurodevelopmental approaches given the prior work done in this area rather than a social psychology framework that is not directly evaluated.

We appreciate the reviewer’s thoughtful and constructive feedback. We agree that the current study does not directly test mechanisms central to Bandura’s social learning theory, such as observational learning over time or behavioral modeling. In light of this, we have significantly revised the theoretical framing of the manuscript to focus more directly on the biobehavioral synchrony framework, which more accurately reflects the dyadic neural measures employed in this study and is better supported by our findings.

Specifically, we have expanded the Discussion to contextualize our findings in terms of biobehavioral synchrony, emphasizing how inter-subject neural synchronization may reflect coordinated parent-child engagement and emotional attunement. We have also incorporated insights from neurodevelopmental and neuroconstructivist models, acknowledging that social cognitive development is shaped by dynamic interactions between neural maturation and environmental input over time.

Although we continue to briefly reference Bandura’s theory to situate our findings within broader social-cognitive frameworks, we have clearly delineated the boundaries of what our data can support and have tempered previous claims. These changes are intended to better align our conceptual framing with the empirical evidence and relevant theoretical models.

The corresponding changes have been made on pages 11-12 of the revised manuscript.

“Insights into mechanisms of Neuroconstructivist Perspectives and Bandura’s social learning theory

Our findings align with a neuroconstructivist perspective, which conceptualizes brain development as an emergent outcome of reciprocal interactions between biological constraints and context-specific environmental inputs. Rather than presuming fixed traits or linear maturation, this perspective highlights how neural circuits adaptively organize in response to experience, gradually supporting increasingly complex cognitive functions49. It offers a particularly powerful lens for understanding how early caregiving environments modulate the maturation of social brain networks.

Building on this framework, the present study reveals that moment-to-moment neural synchrony between parent and child, especially during emotionally salient or socially meaningful moments, is associated with enhanced Theory of Mind performance and reduced dyadic conflict. This suggests that beyond age-dependent neural maturation, dyadic neural coupling may serve as a relational signal, embedding real-time interpersonal dynamics into the child’s developing neural architecture [1] . Our data demonstrate that children’s brains are not merely passively maturing, but are also shaped by the relational texture of their lived experiences—particularly interactions characterized by emotional engagement and joint attention. Importantly, this adds a new dimension to neuroconstructivist theory: it is not simply whether the environment shapes development, but how the quality of interpersonal input dynamically calibrates neural specialization. Interpersonal variation leaves detectable signatures in the brain, and our use of neural synchrony as a dyadic metric illustrates one potential pathway through which caregiving relationships exert formative influence on the developing social brain.

The contribution of this work lies not in reiterating the interplay of nature and nurture, but in specifying the mechanistic role of interpersonal neural alignment as a real-time, context-sensitive developmental input. Neural synchrony between parent and child may function as a form of relationally grounded, temporally structured experience that tunes the child’s social brain toward contextually relevant signals. Unlike generalized enrichment, this form of neural alignment is inherently personalized and contingent—features that may be especially potent in shaping social cognitive circuits during early childhood.

Although our study was not designed to directly examine learning mechanisms such as imitation or reinforcement, the findings can be viewed as broadly consistent with social learning theory. Bandura's theory posits that human behavior is shaped by observational learning and modeling from others in one's environment [2-4]. According to Bandura, children acquire social cognitive skills by observing and interacting with their parents and other significant figures in their environment. This dynamic interplay shapes their ability to understand and predict the behavior of others, which is crucial for the development of ToM and other social competencies.”

References

(1) Hughes, C. et al. Origins of individual differences in theory of mind: From nature to nurture? Child development 76, 356-370 (2005).

(2) Koole, S. L. & Tschacher, W. Synchrony in psychotherapy: A review and an integrative framework for the therapeutic alliance. Frontiers in psychology 7, 862 (2016).

(3) Liu, D., Wellman, H. M., Tardif, T. & Sabbagh, M. A. Theory of mind development in Chinese children: a meta-analysis of false-belief understanding across cultures and languages. Developmental Psychology 44, 523 (2008).

(4) Frith, U. & Frith, C. D. Development and neurophysiology of mentalizing. Philosophical Transactions of the Royal Society of London. Series B: Biological Sciences 358, 459-473 (2003).

The significance and impact of the findings would be clearer if the authors more clearly situated the findings in the context of (a) other movie and theory of mind fMRI task data during development; and (b) existing data on parent-child neural synchrony (often uses fNIRS or EEG). What principles of brain and social cognition development do these data speak to? What is new?

We thank the reviewer for this thoughtful comment. In response, we have revised the Discussion section to more clearly situate our findings within two key literatures: (a) fMRI studies examining Theory of Mind using movie-based and traditional task paradigms across development, and (b) research on parent-child neural synchrony. We now articulate more explicitly how our findings advance current understanding of the neural architecture of social cognition in childhood, and how they contribute new insights into the relational processes shaping brain function. These revisions clarify the conceptual and empirical novelty of our study, particularly in its use of naturalistic fMRI, simultaneous child-parent dyads, and integration of neural maturity with interpersonal synchrony.

The corresponding changes have been made on pages 12 of the revised manuscript.

“Our findings contribute to and extend prior research using fMRI paradigms to investigate ToM development in children.  Previous work has shown that these networks become increasingly specialized and differentiated throughout childhood [1-3]. The current study extends these findings by demonstrating that the development of social brain networks is a gradual process that continues beyond the preschool years and is related to children's chronological age. This finding is consistent with behavioral research indicating that ToM and social abilities continue to develop and refine throughout middle childhood and adolescence [4]. Importantly, we move beyond prior work by combining reverse correlation with naturalistic stimuli to isolate discrete, behaviorally meaningful events (e.g., mental state attribution, social rejection) and relate children’s brain responses to adult patterns and social outcomes. This event-level analysis in a dyadic context offers greater ecological and interpretive precision than traditional block or condition-based designs. Our study provides novel evidence for the neural underpinnings of this protracted development, suggesting that the functional maturation of social brain networks may support the continued acquisition and refinement of social cognitive skills.

In parallel, our study builds on and extends a growing body of work on parent-child neural synchrony, much of which has relied on fNIRS or EEG hyperscanning to demonstrate interpersonal alignment during communication, shared attention, or cooperative tasks [5-7]. While these modalities offer fine temporal resolution, they are limited in spatial precision and typically focus on surface-level cortical regions such as the prefrontal cortex. By contrast, our naturalistic fMRI approach enables the examination of deep and distributed brain networks—specifically those supporting social cognition—within child-parent dyads during emotionally and cognitively rich scenarios. Intriguingly, we found that neural synchronization during movie viewing was higher in child-mother dyads compared to child-stranger dyads.”

Reference

(1) Jacoby, N., Bruneau, E., Koster-Hale, J. & Saxe, R. Localizing Pain Matrix and Theory of Mind networks with both verbal and non-verbal stimuli. Neuroimage 126, 39-48 (2016).

Astington, J. W. & Jenkins, J. M. A longitudinal study of the relation between language and theory-of-mind development. Developmental Psychology 35, 1311 (1999).

(2) Carter, E. J. & Pelphrey, K. A. School-aged children exhibit domain-specific responses to biological motion. Social Neuroscience 1, 396-411 (2006).

(3) Cantlon, J. F., Pinel, P., Dehaene, S. & Pelphrey, K. A. Cortical representations of symbols, objects, and faces are pruned back during early childhood. Cerebral Cortex 21, 191-199 (2011).

(4) Im-Bolter, N., Agostino, A. & Owens-Jaffray, K. Theory of mind in middle childhood and early adolescence: Different from before? Journal of experimental child psychology 149, 98-115 (2016).

(5) Deng, X. et al. Parental involvement affects parent-adolescents brain-to-brain synchrony when experiencing different emotions together: an EEG-based hyperscanning study. Behavioural brain research 458, 114734 (2024).

(6) Miller, J. G. et al. Inter-brain synchrony in mother-child dyads during cooperation: an fNIRS hyperscanning study. Neuropsychologia 124, 117-124 (2019).

(7) Nguyen, T., Bánki, A., Markova, G. & Hoehl, S. Studying parent-child interaction with hyperscanning. Progress in brain research 254, 1-24 (2020).

There is little discussion about the study limitations, considerations about the generalizability of the findings, and important next steps and future directions. What can the data tell us, and what can it NOT tell us?

We appreciate the reviewer’s recommendation to elaborate on the study’s limitations, generalizability, and future directions. In response, we have added a dedicated section to the Discussion that critically addresses these considerations. We acknowledge the cross-sectional nature of the study, the modest sample size, and the use of a single stimulus context as key limitations. We also clarify the inferences that can be drawn from our data and what remains speculative. Finally, we outline specific future research directions.

The corresponding changes have been made on pages 13-14 of the revised manuscript.

“While leveraging a naturalistic movie-viewing paradigm allowed us to study children's spontaneous neural responses during a semi-structured yet engaging task, dedicated experimental designs are still needed to make stronger inferences about the cognitive processes involved. Additionally, our region-of-interest approach precluded examination of whole-brain networks; future work could explore developmental changes in broader functional circuits. The cross-sectional nature of our study is a further limitation, as it cannot definitively establish the causal directions of the observed relationships. Longitudinal designs tracking children's brain development and social cognitive abilities over time would help clarify whether early parenting impacts later neural maturation and behavioral outcomes, or vice versa. Our sample was restricted to mother-child dyads, leaving open questions about potential differences in father-child relationships and gender effects on parenting neurobiology. Larger and more diverse samples would enhance the generalizability of the findings.

Several future directions emerge from this research. First, combining naturalistic neuroimaging with structured cognitive tasks could elucidate the specific mental processes underlying children's neural responses during movie viewing. Examining how these processes relate to real-world social behavior would further bridge neurocognitive function and ecological validity. Longitudinal studies beginning in infancy could chart the developmental trajectories of parent-child neural synchrony and their impact on long-term social outcomes. Such work could also explore sensitive periods when parenting may be most influential on social brain maturation. Finally, expanding this multimodal approach to clinical populations like autism could yield insights into atypical social cognitive development and inform tailored intervention strategies targeting parent-child relationships and neural plasticity.”

To evaluate associations between child neural activity patterns during the movie AND parent-child synchronization patterns AND other variables such as parent-child communication and theory of mind behavior, it seems like a robust approach could be to examine whether similar synchronization patterns are associated with similar scores on different variables. Would allow for non-linear and multivariate associations.

We greatly appreciate the reviewer’s thoughtful suggestion regarding the use of similarity-based or multivariate analyses to assess whether dyads with similar neural synchronization profiles also exhibit similar scores on behavioral or relational variables. We agree that this type of analysis—such as representational similarity analysis (RSA) or inter-subject pattern similarity—offers a powerful framework for capturing non-linear and multivariate associations, and could provide deeper insights into shared neurobehavioral patterns across participants. However, the analytic logic of similarity-based approaches typically requires the availability of comparable measures across individuals or dyads (e.g., child A and child B must both have measures of brain activity, behavior, and environment). In the present study, our focus was on the child as the behavioral and developmental target, and we did not collect parallel behavioral or cognitive variables from the parent side (e.g., adult Theory of Mind ability, emotional traits, parenting style questionnaires beyond dyadic reports). As a result, it was not feasible to construct pairwise similarity matrices across dyads that include both neural synchrony and matched behavioral dimensions from both individuals.

Instead, our study was designed to examine how child-level outcomes (e.g., Theory of Mind performance, social functioning) are associated with (a) the child’s neural responses to specific social events, and (b) the degree of neural synchronization with their mother, as a marker of relational engagement. The analytical emphasis, therefore, remained on within-child variation, modulated by the quality of the parent-child interaction.

Were there associations between parent-child neural synchronization and child age? What was the association between neural maturity and parent-child neural synchronization

We thank the reviewer for raising this important point regarding associations between parent-child neural synchronization (ISS), child age, and neural maturity.

As reported in the original manuscript, we did not observe significant correlations between parent-child ISS and child age for either the Theory of Mind (ToM) or Social Pain Matrix (SPM) networks (all ps > 0.1). Additionally, we conducted additional analysis, we found no significant correlations between ISS and neural maturity (Author response image 1, r = 0.2503, p = 0.1533).

These findings indicate that parent-child neural synchronization in this naturalistic viewing context is not simply explained by age-related maturation or children's neural maturity level. Instead, ISS may predominantly reflect real-time interpersonal engagement or relational dynamics rather than individual developmental trajectories or neural maturity.

Author response image 1.

Scatterplot showing the association between parent-child inter-subject synchronization (ISS) and neural maturity, averaged across the Theory of Mind (ToM) and Social Pain Matrix (SPM) networks. Each point represents one dyad. No significant correlation was observed between ISS and neural maturity (r = 0.2503, p = 0.1533, suggesting that interpersonal neural synchronization and individual neural maturation may reflect dissociable aspects of social brain development.

The rationale for splitting the ages into 3 groups is unclear and creates small groups that could be more prone to spurious associations. Why not look at age continuously?

We thank the reviewer for raising this important point. We fully agree that analyzing age as a continuous variable is statistically more robust and minimizes concerns about spurious associations due to arbitrary groupings.

To clarify, all primary statistical models—including correlational analyses—treated age as a continuous variable, and our core developmental inferences are based on these continuous-age findings.

In addition to these analyses, we included age group comparisons as a supplementary approach, guided by both theoretical considerations and visual inspection of the data. Specifically, we aimed to explore whether functional differentiation between social brain networks (e.g., ToM and SPM) might begin to emerge non-linearly or earlier than expected, particularly in the youngest children. Such early neural divergence may not be well-captured by linear trends alone. The grouped analysis allowed us to illustrate that network differentiation was already observable in children under age 5, suggesting that certain aspects of social brain organization may emerge earlier than classically assumed.

We have now clarified this rationale in the revised manuscript and emphasized that the group-based analysis was used solely to highlight developmental shifts that may not follow a linear pattern, and not for formal hypothesis testing.

The corresponding changes have been made on pages 9 of the revised manuscript.

“While our primary analyses treated age as a continuous variable, we also performed exploratory group-based comparisons to probe for potential non-linear developmental shifts in social brain network organization. This approach revealed that the differentiation between ToM and SPM networks was already present in the youngest group (ages 3–4), suggesting that early neural specialization may begin prior to the age at which ToM behavior is reliably observed. These group-level observations provide complementary evidence to the continuous analyses and may inform future work examining sensitive periods or early markers of social brain development.”

Tables would be improved if they were more professionally formatted (e.g., names of the variables rather than variable abbreviation codes).

We appreciate the reviewer’s suggestion to improve the clarity and professionalism of our tables. In the revised manuscript, we have reformatted all tables to include full variable names rather than abbreviations or coded labels, and we ensured consistency in terminology across the manuscript text, tables, and figure legends. We have also added explanatory footnotes where needed to clarify any derived or composite measures. We hope these revisions improve the accessibility and readability of the results for a broader audience

Reviewer #2:

Summary:

This study investigates the impact of mother-child neural synchronization and the quality of parent-child relationships on the development of Theory of Mind (ToM) and social cognition. Utilizing a naturalistic fMRI movie-viewing paradigm, the authors analyzed inter-subject neural synchronization in mother-child dyads and explored the connections between neural maturity, parental caregiving, and social cognitive outcomes. The findings indicate age-related maturation in ToM and social pain networks, emphasizing the importance of dyadic interactions in shaping ToM performance and social skills, thereby enhancing our understanding of the environmental and intrinsic influences on social cognition.

Strengths:

This research addresses a significant question in developmental neuroscience, by linking social brain development with children's behaviors and parenting. It also uses a robust methodology by incorporating neural synchrony measures, naturalistic stimuli, and a substantial sample of mother-child dyads to enhance its ecological validity. Furthermore, the SEM approach provides a nuanced understanding of the developmental pathways associated with Theory of Mind (ToM).

We appreciate the positive evaluation and valuable comments of the reviewer. According to the reviewer`s comments, we have revised the manuscript thoroughly to address the concerns raised by the reviewer. A point-by-point response to each of the issues raised by the reviewer has been made. We believe that the revision of our manuscript has now been significantly improved.

Upon reviewing the introduction, I feel that the first goal - developmental changes of the social brain and its relation to age - seems somewhat distinct from the other two goals and the main research question of the manuscript. The authors might consider revising this section to enhance the overall coherence of the manuscript. Additionally, the introduction lacks a clear background and rationale for the importance of examining age-related changes in the social brain.

We thank the reviewer for this thoughtful observation. In response, we have revised the Introduction to better integrate the developmental aspect of the social brain with the broader research aims. We now explicitly link age-related changes in social brain organization to the emergence of social cognitive abilities and highlight why early childhood (ages 3–8) represents a particularly formative period. This revision clarifies that our first aim—examining functional specialization and neural maturity in Theory of Mind (ToM) and Social Pain Matrix (SPM) networks—serves as a developmental foundation for understanding how dyadic influences, such as neural synchrony and caregiving quality, shape children’s social cognition.

We have also improved the rationale for examining age-related change, drawing on key literature in developmental neuroscience to show how the early emergence and specialization of social brain networks provide a necessary context for interpreting interpersonal neural dynamics.

The corresponding changes have been made on pages 3 of the revised manuscript.

“These findings suggest that the development of specialized brain regions for reasoning about others' mental states and physical sensations is a gradual process that continues throughout childhood.

Understanding how these networks differentiate with age is essential not only for mapping typical brain development, but also for contextualizing the role of environmental influences. By establishing normative patterns of neural maturity and differentiation, we can better interpret how relational experiences—such as caregiver-child synchrony and parenting quality—modulate these trajectories. Thus, our first goal provides a developmental anchor that grounds our investigation of interpersonal and environmental contributions to social brain function.”

The manuscript uses both "mother-child" and "parent-child" terminology. Does this imply that only mothers participated in the fMRI scans while fathers completed the questionnaires? If so, have the authors considered the potential impact of parental roles (father vs. mother)?

We thank the reviewer for raising this important point regarding terminology and parental roles. To clarify, all participating caregivers in the current study were biological mothers, and all behavioral questionnaires were also completed by these same mothers. No fathers were included in this study. We have revised the manuscript throughout to consistently use the term “mother-child” when referring to the specific dyads in our sample.

We also appreciate the opportunity to elaborate on the rationale for including only mothers. Prior research has shown that maternal and paternal influences on child development are not interchangeable, and that the neural correlates of caregiving behaviors differ between mothers and fathers. For example, studies have demonstrated distinct patterns of brain activation during social and emotional processing in mothers versus fathers (Abraham et al., 2014; JE Swain et al., 2014). Given these differences, we deliberately focused on mother-child dyads to maintain neurobiological consistency in our analysis and reduce variance associated with heterogeneous caregiving roles. We now clarify this rationale in the revised Methods and Discussion sections.

The corresponding changes have been made on pages 14 of the revised manuscript.

“We chose to focus exclusively on mother-child dyads in this study based on prior evidence suggesting distinct neural and behavioral caregiving profiles between mothers and fathers [1-2], allowing us to maintain role consistency and reduce variability in dyadic interactions.

Our sample was restricted to mother-child dyads, leaving open questions about potential differences in father-child relationships and gender effects on parenting neurobiology [1]. Larger and more diverse samples would enhance the generalizability of the findings.”

Reference:

(1) Swain, J. E. et al. Approaching the biology of human parental attachment: Brain imaging, oxytocin and coordinated assessments of mothers and fathers. Brain research 1580, 78-101 (2014).

(2) Abraham, E. et al. Father's brain is sensitive to childcare experiences. Proceedings of the National Academy of Sciences 111, 9792-9797 (2014).

There is inconsistent usage of the terms ISC and ISS in the text and figures, both of which appear to refer to synchronization derived from correlation analysis. It would be beneficial to maintain consistency throughout the manuscript.

We thank the reviewer for highlighting the inconsistent use of “ISC” and “ISS” in the original manuscript. We agree that clarity and consistency in terminology are essential. In response, we have revised the manuscript to consistently use “ISS” (inter-subject synchronization) throughout the text, figures, tables, and legends.

Of the 50 dyads, 16 were excluded due to data quality issues, which constitutes a significant proportion. It would be helpful to know whether these excluded dyads exhibited any distinctive characteristics. Providing information on demographic or behavioral differences-such as Theory of Mind (ToM) performance and age range between the excluded and included dyads would enhance the assessment of the findings' generalizability.

We thank the reviewer for this important observation. We agree that understanding the characteristics of excluded participants is essential for assessing the generalizability of the findings.

In response, we conducted comparative analyses between included and excluded dyads (N = 34 included; N = 16 excluded) on key demographic and behavioral variables, including child age, gender, and Theory of Mind (ToM) performance. These analyses revealed no significant differences between groups on any of these measures (ps > 0.1), suggesting that data exclusion due to quality issues (e.g., excessive motion, incomplete scans) did not introduce systematic bias.

We have now added this information to the Results and Methods sections of the manuscript.

The corresponding changes have been made on pages 6 and 17 of the revised manuscript.

“Of the 50 initial mother-child dyads recruited, 16 were excluded due to excessive head motion (n = 11), incomplete scan sessions (n = 3), or technical issues during data acquisition (n = 2). The final sample consisted of 34 dyads. To assess potential bias introduced by data exclusion, we compared included and excluded dyads on child age, gender, and Theory of Mind performance. No significant differences were found across these variables (all ps > 0.1), suggesting that the analytic sample was demographically representative of the full cohort.

Comparison between included and excluded dyads revealed no significant differences in child age (t = 1.23, p = 0.24), ToM scores (t = -0.54, p = 0.59), or sex distribution (χ² < 0.01, p = 0.98), indicating that data exclusion did not bias the sample in a systematic way.”

The article does not adhere to the standard practice of using a resting state as a baseline for subtracting from task synchronization. Is there a rationale for this approach? Not controlling for a baseline may lead to issues, such as whether resting state synchronization already differs between subjects with varying characteristics.

We thank the reviewer for raising this important methodological point. We agree that controlling for baseline synchronization, such as using a resting-state scan as a comparison, can help disambiguate whether task-induced synchrony reflects genuine stimulus-driven coupling or baseline differences across individuals or dyads.

In the present study, we focused on inter-subject synchronization (ISS) during naturalistic movie viewing, a task condition that has been widely used in previous developmental and social neuroscience research to assess shared neural engagement. We did not include a resting-state scan in the current protocol due to time constraints and the young age of our participants (ages 3–8), as longer scanning sessions often result in increased motion and reduced data quality in pediatric populations. Moreover, many prior studies using ISS in naturalistic paradigms have similarly focused on task-driven synchrony without subtracting a resting baseline (e.g., Hasson et al., 2004; Nguyen et al., 2020; Reindl et al., 2018).

That said, we acknowledge that baseline neural synchrony across dyads may vary depending on individual or relational characteristics (e.g., temperament, arousal, attentional style), and this remains an important question for future research. In the revised Discussion, we now explicitly note the absence of a resting-state baseline as a limitation and highlight the need for future studies to examine how resting and task-based ISS may interact, particularly in the context of child-caregiver dyads.

The corresponding changes have been made on page 13 of the revised manuscript.

“Another limitation of the current design is the lack of a resting-state baseline for inter-subject synchronization. While our focus was on synchronization during naturalistic social processing, we cannot determine whether individual differences in ISS reflect purely task-induced coupling or are partially shaped by trait-level synchrony present at rest. Including both resting and task conditions in future work would allow for stronger inferences about stimulus-specific versus baseline-driven synchronization, especially in relation to interpersonal factors such as relationship quality or social responsiveness.”

The title of the manuscript suggests a direct influence of mother-child interactions on children's social brain and theory of mind. However, the use of structural equation modeling (SEM) may not fully establish causal relationships. It is possible that the development of children's social brain and ToM also enhances mother-child neural synchronization. The authors should address this alternative hypothesis of the potential bidirectional relationship in the discussion and exercise caution regarding terms that imply causality in the title and throughout the manuscript.

We appreciate the reviewer’s careful attention to issues of causality in our manuscript. We agree that our cross-sectional design limits causal inference, and that the use of structural equation modeling (SEM) in this context does not allow for conclusions about directional or mechanistic pathways. In response, we have revised the Discussion to explicitly acknowledge these limitations, and now include an expanded section on the potential for bidirectional or co-constructed processes, consistent with neuroconstructivist frameworks.

We have also tempered the interpretation of our SEM findings, avoiding causal language throughout the manuscript and clarifying that our analyses are exploratory and associational in nature. We hope that these changes provide a more cautious and developmentally grounded interpretation of the data.

With regard to the title, we respectfully chose to retain the original wording, as we believe it captures the thematic focus and central research question of the paper—namely, the potential role of mother-child interaction in the development of children’s social brain and Theory of Mind. While we understand the reviewer’s concern, we note that the interpretation of this phrasing is contextualized within the manuscript, which now includes clear qualifications regarding the limits of causal inference. We have taken care to ensure that no claims of unidirectional causality are made in the body of the paper.

The corresponding changes have been made on pages 11- 12 of the revised manuscript.

“Our findings align with a neuroconstructivist perspective, which conceptualizes brain development as an emergent outcome of reciprocal interactions between biological constraints and context-specific environmental inputs. Rather than presuming fixed traits or linear maturation, this perspective highlights how neural circuits adaptively organize in response to experience, gradually supporting increasingly complex cognitive functions54. It offers a particularly powerful lens for understanding how early caregiving environments modulate the maturation of social brain networks.

Building on this framework, the present study reveals that moment-to-moment neural synchrony between parent and child, especially during emotionally salient or socially meaningful moments, is associated with enhanced Theory of Mind performance and reduced dyadic conflict. This suggests that beyond age-dependent neural maturation, dyadic neural coupling may serve as a relational signal, embedding real-time interpersonal dynamics into the child’s developing neural architecture. Our data demonstrate that children’s brains are not merely passively maturing, but are also shaped by the relational texture of their lived experiences—particularly interactions characterized by emotional engagement and joint attention. Importantly, this adds a new dimension to neuroconstructivist theory: it is not simply whether the environment shapes development, but how the quality of interpersonal input dynamically calibrates neural specialization. Interpersonal variation leaves detectable signatures in the brain, and our use of neural synchrony as a dyadic metric illustrates one potential pathway through which caregiving relationships exert formative influence on the developing social brain.

The contribution of this work lies not in reiterating the interplay of nature and nurture, but in specifying the mechanistic role of interpersonal neural alignment as a real-time, context-sensitive developmental input. Neural synchrony between parent and child may function as a form of relationally grounded, temporally structured experience that tunes the child’s social brain toward contextually relevant signals. Unlike generalized enrichment, this form of neural alignment is inherently personalized and contingent—features that may be especially potent in shaping social cognitive circuits during early childhood.

The cross-sectional nature of our study is a further limitation, as it cannot definitively establish the causal directions of the observed relationships. Longitudinal designs tracking children's brain development and social cognitive abilities over time would help clarify whether early parenting impacts later neural maturation and behavioral outcomes, or vice versa.”

I would appreciate more details about the 14 Theory of Mind (ToM) tasks, which could be included in supplemental materials. The authors score them on a scale from 0 to 14 (each task 1 point); however, the tasks likely vary in difficulty and should carry different weights in the total score (for example, the test and the control questions should have different weights). Many studies have utilized the seven tasks according to Wellman and Liu (2004), categorizing them into "basic ToM" and "advanced ToM." Different components of ToM could influence the findings of the current study, which should be further examined by a more in-depth analysis.

We thank the reviewer for raising this important point regarding the structure and scoring of the Theory of Mind (ToM) tasks. We will provide a detailed description of all 14 tasks in the Supplemental Materials, including their content, targeted mental state concepts (e.g., beliefs, desires, intentions), and design features (e.g., test/control items, task format).

We fully agree that ToM tasks differ in complexity, and in principle, a weighted or component-based scoring approach (e.g., distinguishing basic and advanced ToM) could offer greater interpretive value. However, in our study design, tasks were administered in a fixed sequence from lower to higher difficulty, and testing was terminated if the child was unable to successfully complete three consecutive tasks. This approach is developmentally appropriate for younger children but results in non-random missingness for more advanced tasks—particularly among children at the lower end of the age range (3–4 years).

Given this adaptive task structure, re-scoring using weighted or subscale-based approaches would introduce systematic bias, as children who struggled with early items were not administered more complex ones. As a result, a full breakdown by task type (e.g., basic vs. advanced ToM) would only reflect a restricted subsample and would not be comparable across the full cohort. For this reason, we retained the unit-weighted total ToM score as the most developmentally valid and comparable metric across participants.

Reviewer #3:

Summary:

The article explores the role of mother-child interactions in the development of children's social cognition, focusing on Theory of Mind (ToM) and Social Pain Matrix (SPM) networks. Using a naturalistic fMRI paradigm involving movie viewing, the study examines relationships among children's neural development, mother-child neural synchronization, and interaction quality. The authors identified a developmental pattern in these networks, showing that they become more functionally distinct with age. Additionally, they found stronger neural synchronization between child-mother pairs compared to child-stranger pairs, with this synchronization and neural maturation of the networks associated with the mother-child relationship and parenting quality.

Strengths:

This is a well-written paper, and using dyadic fMRI and naturalistic stimuli enhances its ecological validity, providing valuable insights into the dynamic interplay between brain development and social interactions. However, I have some concerns regarding the analysis and interpretation of the findings. I have outlined these concerns below in the order they appear in the manuscript, which I hope will be helpful for the revision.

We appreciate the reviewer’s thoughtful and constructive summary of the manuscript. The concerns raised regarding aspects of the analysis and interpretation have been carefully considered. Detailed point-by-point responses are provided below, along with descriptions of the corresponding revisions made to improve the clarity, precision, and interpretive caution of the manuscript.

Given the importance of social cognition in this study, please cite a foundational empirical or review paper on social cognition to support its definition. The current first citation is primarily related to ASD research, which may not fully capture the broader context of social cognition development.

We thank the reviewer for this helpful suggestion. We agree that a broader, foundational reference is more appropriate for introducing the concept of social cognition. In response, we have revised the Introduction to include a widely cited theoretical or review paper on social cognition to provide a more general developmental context.

The corresponding changes have been made on pages 3 of the revised manuscript.

“Social cognition, defined as the ability to interpret and predict others' behavior based on their beliefs and intentions and to interact in complex social environments and relationships is a crucial aspect of human development [1-2]”

(1) Adolphs, R. The social brain: neural basis of social knowledge. Annual review of psychology 60, 693-716 (2009).

(2) Frith, C. D. & Frith, U. Mechanisms of social cognition. Annual review of psychology 63, 287-313 (2012).

It is standard practice to report the final sample size in the Abstract and Introduction, rather than the initial recruited sample, as high attrition rates are common in pediatric studies. For example, this study recruited 50 mother-child dyads, and only 34 remained after quality control. This information is crucial for interpreting the results and conclusions. I recommend reporting the final sample size in the abstract and introduction but specifying in the Methods that an additional 16 mother-child dyads were initially recruited or that 50 dyads were originally collected.

We thank the reviewer for this helpful recommendation. In the original version of the manuscript, the Abstract and Introduction referenced the total number of dyads recruited (N = 50). In line with standard reporting practices and to ensure clarity regarding the analytic sample, we have now revised both the Abstract and Introduction to report the final sample size (N = 34). The full recruitment and exclusion details—including the number of dyads removed due to excessive motion or technical issues—are now clearly described in the Methods section.

The corresponding changes have been made on pages 1 and 4 of the revised manuscript.

In the "Neural maturity reflects the development of the social brain" section, the authors report the across-network correlation for adults, finding a negative correlation between ToM and SPM. However, the cross-network correlations for the three child groups are not reported. The statement that "the two networks were already functionally distinct in the youngest group of children we tested" is based solely on within-network positive correlations, which does not fully demonstrate functional distinctness. Including cross-network correlations for the child groups would strengthen this conclusion.

We thank the reviewer for this insightful comment. We agree that within-network correlations alone do not fully establish functional distinctness, particularly in early development. To more directly test whether the ToM and SPM networks were already differentiated in children, we have now included the cross-network correlations between the two networks for each of the three age groups in the revised manuscript. These findings support and strengthen our original claim that the ToM and SPM networks are functionally dissociable even in early childhood, and we have revised the relevant Results sections accordingly to reflect this.

The corresponding changes have been made on page 7 of the revised manuscript.

“In children, each network also exhibited positive correlations within-network and negative correlations across networks (within-ToM correlation M(s.e.) = 0.31(0.04); within-SPM correlation M(s.e.) = 0.29(0.04); across-network M(s.e.) = −0.09 (0.02).

In the Pre-junior group only (3-4 years old children, n = 12), both ToM and SPM networks had positive within-network correlations (within-ToM correlation M (s.e.) = 0.29(0.06); within-SPM correlation M(s.e.) = 0.23(0.05), across-network M(s.e.) = −0.05(0.02)).”

The ROIs for the ToM and SPM networks are defined based on previous literature, applying the same ROIs across all age groups. While I understand this is a common approach, it's important to note that this assumption may not fully hold, as network architecture can evolve with age. The functional ROIs or components of a network might shift, with regions potentially joining or exiting a network or changing in size as children develop. For instance, Mark H. Johnson's interactive specialization theory suggests that network composition may adapt over developmental stages. Although the authors follow the approach of Richardson et al. (2018), it would be beneficial to discuss this limitation in the Discussion. An alternative approach would be to apply data-driven analysis to justify the selection of the ROIs for the two networks.

We thank the reviewer for this thoughtful and theoretically grounded comment.  In our study, we followed the approach of Richardson et al. (2018), using a priori ROIs defined from adult meta-analyses and ToM/SPM task studies. This approach facilitates comparison with prior work and provides anatomical consistency across participants. However, we fully agree that applying adult-defined ROIs to pediatric populations involves important assumptions about the stability of network architecture across development, which may not fully hold in early childhood.

We have now addressed this limitation more explicitly in the revised Discussion, emphasizing that the fixed-ROI approach may not capture the dynamic reorganization of social brain networks during development.

The corresponding changes have been made on pages 13 of the revised manuscript.

“Moreover, the ROIs used to define the ToM and SPM networks were based on meta-analyses and task studies primarily conducted with adults. While this approach promotes comparability with existing literature, it assumes that the spatial organization of these networks is stable across age groups. However, theories of interactive specialization suggest that the composition and boundaries of functional networks may undergo reorganization during development, with regions potentially entering or exiting networks based on experience and maturational processes. As a result, the current analysis may not fully capture age-specific functional architecture, particularly in younger children. Future studies using data-driven or age-appropriate parcellation methods could provide more precise characterizations of how social brain networks are constructed and differentiated throughout childhood.”

The current sample size (N = 34 dyads) is a limitation, particularly given the use of SEM, which generally requires larger samples for stable results. Although the model fit appears adequate, this does not guarantee reliability with the current sample size. I suggest discussing this limitation in more detail in the Discussion.

We thank the reviewer for highlighting the limitations of applying structural equation modeling (SEM) with a relatively modest sample size. We agree that SEM generally benefits from larger samples to ensure model stability and parameter reliability, and that satisfactory model fit does not guarantee robustness in small-sample contexts.

In the revised Discussion, we now more clearly acknowledge that the use of SEM in the current study is exploratory in nature, and that all results should be interpreted with caution due to potential sample size-related constraints. The model was constructed to provide an integrated view of the observed associations rather than to establish definitive pathways. We have also added a note that future research with larger samples and longitudinal designs will be needed to validate and extend the proposed model.

The corresponding changes have been made on pages 13 of the revised manuscript.

“In addition, the modest sample size (N = 34 dyads) presents limitations for the application of structural equation modeling (SEM), which typically requires larger samples for stable estimation and generalizable inferences. While the model fit was acceptable, the results should be interpreted as exploratory and hypothesis-generating, rather than confirmatory. Future studies with larger, independent samples will be important for validating the structure and directionality of the proposed relationships”

Based on the above comment, I believe that conclusions regarding the relationship between social network development, parenting, and support for Bandura's theory should be tempered. The current conclusions may be too strong given the study's limitations.

We thank the reviewer for this important and balanced observation. We agree that the conclusions drawn from the current study should reflect the exploratory nature of the analyses, as well as the methodological limitations, including the modest sample size and cross-sectional design.

In response, we have revised the Conclusion sections to use more cautious, associative language when describing the observed relationships among social brain development, parenting factors, and Theory of Mind outcomes. In particular, we have tempered statements regarding support for Bandura’s social learning theory, clarifying that while our findings are consistent with social learning frameworks, the data do not allow for direct tests of modeling or observational learning mechanisms.

We hope these revisions help clarify the scope of the findings and improve the conceptual rigor of the manuscript.

The corresponding changes have been made on pages 14 of the revised manuscript.

“Our study provides novel evidence that children's social cognitive development may be shaped by the intricate interplay between environmental influences, such as parenting, and biological factors, such as neural maturation. Our findings contribute to a growing understanding of the factors associated with social cognitive development and suggest the potential importance of parenting in this process. Specifically, the study points to the possible role of the parent-child relationship in supporting the development of social brain circuitry and highlights the relevance of family-based approaches for addressing social difficulties. The observed neural synchronization between parent and child, which was associated with relationship quality, underscores the potential significance of positive parental engagement in fostering social cognitive skills. Future longitudinal and clinical research can build on this multimodal approach to further clarify the neurobehavioral mechanisms underlying social cognitive development. Such research may help inform more effective strategies for promoting healthy social functioning and mitigating social deficits through targeted family-based interventions.”

The SPM (pain) network is associated with empathic abilities, also an important aspect of social skills. It would be relevant to explore whether (or explain why) SPM development and child-mother synchronization are (or are not) related to parenting and the parent-child relationship.

We thank the reviewer for this thoughtful and important comment regarding the role of the Social Pain Matrix (SPM) network in social cognition and empathy. We agree that this network represents a critical component of social-cognitive development and is theoretically linked to affective processing and interpersonal understanding.

We would like to clarify that in our existing analyses—already included in the original submission and detailed in the Supplemental Results—SPM network measures showed similar significant associations with behavioral outcomes than the ToM network. These outcomes included children's performance on ToM tasks as well as broader measures of social functioning. We have added more discussion in the supplementary results.

“To further investigate the specificity of our findings, we conducted additional control analyses focusing on the individual components of the social brain networks examined in our study: the Theory of Mind (ToM) and Social Pain Matrix (SPM) networks.

When analyzing these networks separately, we found significant correlations between neural maturity and age, as well as between inter-subject synchronization (ISS) and parent-child relationship quality for both the ToM and SPM networks individually (Fig. S1). Specifically, neural maturity within each network was positively correlated with age, indicating that both networks undergo maturation during childhood. Similarly, ISS within each network was negatively correlated with parent-child conflict scores, suggesting that both networks contribute to the observed relationship between neural synchrony and parent-child relationship quality.

These results highlight the importance of considering the social brain as an integrated system, where the ToM and SPM networks work in concert to support social cognitive development. While each network shows age-related maturation and sensitivity to parent-child relationship quality, their combined functioning appears to be crucial for predicting broader social cognitive outcomes.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

In their paper, Kang et al. investigate rigidity sensing in amoeboid cells, showing that, despite their lack of proper focal adhesions, amoeboid migration of single cells is impacted by substrate rigidity. In fact, many different amoeboid cell types can durotax, meaning that they preferentially move towards the stiffer side of a rigidity gradient.

The authors observed that NMIIA is required for durotaxis and, building on this observation, they generated a model to explain how durotaxis could be achieved in the absence of strong adhesions. According to the model, substrate stiffness alters the diffusion rate of NMAII, with softer substrates allowing for faster diffusion. This allows for NMAII accumulation at the back, which, in turn, results in durotaxis.

The experiments support the main message of the paper regarding durotaxis by amoeboid cells. In my opinion, a few clarifications on the mechanism proposed to explain this phenomenon could strengthen this research:

(1) According to your model, the rear end of the cell, which is in contact with softer substrates, will have slower diffusion rates of MNIIA. Does this mean that bigger cells will durotax better than smaller cells because the stiffness difference between front and rear is higher? Is it conceivable to attenuate the slope of the durotactic gradient to a degree where smaller cells lose their ability to durotact, while longer cells retain their capacity for directional movement?

We thank the reviewer for this comment. In fact, it is not always the case that bigger cells will durotax better than smaller cells. Although bigger cells will sense higher stiffness difference between the front and rear, cells placed on different regions of underlying substrates may respond differently. This is because diffusion coefficient difference is not proportional to stiffness difference in our theoretical model. Therefore, when cells are placed on a very stiff substrate, cells may not durotax. When cells are placed on a region with suitable stiffness, where cells are sensitive to stiffness gradient, bigger cells will durotax better than smaller cells. In this situation, as you mentioned, lowering the stiffness gradient will make smaller cells become adurotactic while longer cells still durotax.

We tried to further address this question by our durotaxis assay but there was a challenge: the amoeboid cells we use, including CD4+ Naïve T cells, neutrophils, dHL-60 cells and Dictysotelium, frequently protrude, retract and alter contact area with the substrate which make it difficult for us to distinguish between bigger and smaller cells in a particular cell type. Previously reported durotactic cell lines, such as MDA-MB-231 and HT1080 cells, are bigger than the amoeboid cells we use but they are mesenchymal cells and adopt distinct mechanisms which always involve stable focal adhesions. Due to this, although we are eager to answer this question by experiments and that the stiffness gradient is tunable in our system, we have not found an appropriate approach and experimental setup.

(2) Where did you place the threshold for soft, middle, and stiff regions (Figure 6)? Is it possible that you only have a linear rigidity gradient in the center of your gel and the more you approach the borders, the flatter the gradient gets? In this case, cells would migrate randomly on uniform substrates. Did you perform AFM over the whole length of the gel or just in the central part?

We thank the reviewer for this comment. We have performed AFM over the whole length of our gradient gel (Fig. S1A). We divide the gel into three equal parts (stiff: 1-4 mm; middle: 4-7 mm; soft: 7-10 mm) and the stiffness gradient is almost linear within each part as shown in Fig. S1A.

(3) In which region (soft, middle, stiff) did you perform all the cell tracking of the previous figures?

We thank the reviewer for this question. We performed the cell tracking in the soft region of the gradient gel.

(4) What is the level of confinement experienced by the cells? Is it possible that cells on the soft side of the gels experience less confinement due to a "spring effect" whereby the coverslips descending onto the cells might exert diminished pressure because the soft hydrogels act as buffers, akin to springs? If this were the case, cells could migrate following a confinement gradient.

We thank the reviewer for this comment. Although the possibility that our thin hydrogel layers act as buffers cannot be completely excluded, we have performed the durotaxis assay without upper gradient gel providing confinement (Author response image 1A). In this case, CD4+ Naïve T cells, neutrophils, dHL-60 cells and Dictysotelium can still durotax (Author response image 1B-E), indicating stiffness gradient itself is sufficient to direct amoeboid cell migration.

Author response image 1.

Illustration of the durotaxis system without confinement (A) and y-FMI of CD4+ Naïve T cells (B), neutrophils (C), dHL-60 cells (D) and Dictysotelium (E) cultured on uniform substrate or gradient substrate (n ≥ 30 tracks were analyzed for each experiment, N = 3 independent experiments for each condition, replicates are biological). All error bars are SEM. ****, P < 0.0001, by Student’s t-test.

Reviewer #2 (Public Review):

Summary:

The authors developed an imaging-based device that provides both spatialconfinement and stiffness gradient to investigate if and how amoeboid cells, including T cells, neutrophils, and Dictyostelium, can durotax. Furthermore, the authors showed that the mechanism for the directional migration of T cells and neutrophils depends on non-muscle myosin IIA (NMIIA) polarized towards the soft-matrix-side. Finally, they developed a mathematical model of an active gel that captures the behavior of the cells described in vitro.

Strengths:

The topic is intriguing as durotaxis is essentially thought to be a direct consequence of mechanosensing at focal adhesions. To the best of my knowledge, this is the first report on amoeboid cells that do not depend on FAs to exert durotaxis. The authors developed an imaging-based durotaxis device that provides both spatial confinement and stiffness gradient and they also utilized several techniques such as quantitative fluorescent speckle microscopy and expansion microscopy. The results of this study have well-designed control experiments and are therefore convincing.

Weaknesses:

Overall this study is well performed but there are still some minor issues I recommend the authors address:

(1) When using NMIIA/NMIIB knockdown cell lines to distinguish the role of NMIIA and NMIIB in amoeboid durotaxis, it would be better if the authors took compensatory effects into account.

We thank the reviewer for this suggestion. We have investigated the compensation of myosin in NMIIA and NMIIB KD HL-60 cells using Western blot and added this result in our updated manuscript (Fig. S4B, C). The results showed that the level of NMIIB protein in NMIIA KD cells doubled while there was no compensatory upregulation of NMIIA in NMIIB KD cells. This is consistent with our conclusion that NMIIA rather than NMIIB is responsible for amoeboid durotaxis since in NMIIA KD cells, compensatory upregulation of NMIIB did not rescue the durotaxis-deficient phenotype.

(2) The expansion microscopy assay is not clearly described and some details are missed such as how the assay is performed on cells under confinement.

We thank the reviewer for this comment. We have updated details of the expansion microscopy assay in our revised manuscript in line 481-485 including how the assay is performed on cells under confinement:

Briefly, CD4+ Naïve T cells were seeded on a gradient PA gel with another upper gel providing confinement. 4% PFA was used to fix cells for 15 min at room temperature. After fixation, the upper gradient PA gel is carefully removed and the bottom gradient PA gel with seeded cells were immersed in an anchoring solution containing 1% acrylamide and 0.7% formaldehyde (Sigma, F8775) for 5 h at 37 °C.

(3) In this study, an active gel model was employed to capture experimental observations. Previously, some active nematic models were also considered to describe cell migration, which is controlled by filament contraction. I suggest the authors provide a short discussion on the comparison between the present theory and those prior models.

We thank the reviewer for this suggestion. Active nematic models have been employed to recapitulate many phenomena during cell migration (Nat Commun., 2018, doi: 10.1038/s41467-018-05666-8.). The active nematic model describes the motion of cells using the orientation field, Q, and the velocity field, u. The director field n with (n = −n) is employed to represent the nematic state, which has head-tail symmetry. However, in our experiments, actin filaments are obviously polarized, which polymerize and flow towards the direction of cell migration. Therefore, we choose active gel model which describes polarized actin field during cell migration. In the discussion part, we have provided the comparison between active gel model and motor-clutch model. We have also supplemented a short discussion between the present model and active nematic model in the main text of line 345-347:

The active nematic model employs active extensile or contractile agents to push or pull the fluid along their elongation axis to simulate cells flowing (61).

(4) In the present model, actin flow contributes to cell migration while myosin distribution determines cell polarity. How does this model couple actin and myosin together?

We thank the reviewer for this question. In our model, the polarization field P(r,t) is employed to couple actin and myosin together. It is obvious that actin accumulate at the front while myosin diffuses in the opposite direction. Therefore, we propose that actin and myosin flow towards the opposite direction, which is captured in the convection term of actin (∇[c(v+wP)])  and myosin (∇[m(-wP)]) density field.

Reviewing Editor (Recommendations For The Authors):

We suggest that you cite the publication about confinement force microscopy from the Betz lab (https://doi.org/10.1101/2023.08.22.554088).

We thank the editor for this suggestion. We have cited this publication in line 89 in our updated manuscript.

Reviewer #1 (Recommendations For The Authors):

Minor points and text corrections:

- In line 288 you state that NMIIA basal diffusion rate is larger on softer substrates, while in line 315 you say that NMIIA is more diffusive on stiff. The two sentences seem to contradict each other.

We thank the reviewer for pointing out this mistake. In our active gel model, the basal diffusion rate of NMIIA is larger on stiffer substrate. We have corrected this mistake in line 288 (line 283 in the updated manuscript) in our revised manuscript.

- How were the non-muscle myosin images (Figure 3F) collected?

We thank the reviewer for this question. The non-muscle myosin images in Fig. 3F are single planes collected by epifluorescence-confocal microscopy. We have updated the related method in our revised manuscript in line 477-478:

After mounting medium is solidified, single plane images were captured using a 63×1.4 NA objective lens on Andor Dragonfly epi-fluorescence confocal imaging system.

- Is there a quantification of NMAII accumulation at the back?

We thank the reviewer for this question. We have a quantification of NMIIA distribution in Fig. 3G. We measured the fluorescence intensity of NMIIA and NMIIB in the soft and stiff region of cells and found that the soft/stiff fluorescence ratio of NMIIB is about 0.95 and the ratio of NMIIA is about 1.82, indicating NMIIA tend to be localized at back while NMIIB is evenly distributed in the soft and stiff region of cells.

- At which frequency were images acquired for Fluorescent Speckle Microscopy? Overall, I think it would help to state the length and frequency of videos in the legends.

We thank the reviewer for this comment. We have updated the length (10 min for movie 6-10 and 80 sec for movie11) and frequency (15 sec intervals for movie 6-10 and 2 sec intervals for movie11) of Fluorescent Speckle Microscopy videos in our revised manuscript.

Reviewer #2 (Recommendations For The Authors):

The cell contour of Figure S5C is not very clear.

We thank the reviewer for this comment. We have marked the outline of the cell in Fig. S5C in our updated manuscript.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this study, Kroll et al. conduct an in-depth behavioral analysis of F0 knockouts of 4 genes associated with late-onset Alzheimer's Disease (AD), together with 3 genes associated with early-onset AD. Kroll and colleagues developed a web application (ZOLTAR) to compare sleep-associated traits between genetic mutants with those obtained from a panel of small molecules to promote the identification of affected pathways and potential therapeutic interventions. The authors make a set of potentially important findings vis-à-vis the relationship between AD-associated genes and sleep. First, they find that loss-of-function in late-onset AD genes universally results in night-time sleep loss, consistent with the well supported hypothesis that sleep disruption contributes to Alzheimer's-related pathologies. psen-1, an early-onset associated AD gene, which the authors find is principally responsible for the generation of AB40 and AB42 in zebrafish, also shows a slight increase in activity at night and slight decreases in night-time sleep. Conversely, psen-2 mutations increase daytime sleep, while appa/appb mutations have no impact on sleep. Finally, using ZOLTAR, the authors identify serotonin receptor activity as potentially disrupted in sorl1 mutants, while betamethasone is identified as a potential therapeutic to promote reversal of psen2 knockout-associated phenotypes.

This is a highly innovative and thorough study, yet a handful of key questions remain. First, are night-time sleep loss phenotypes observed in all knockouts for late-onset AD genes in the larval zebrafish a valid proxy for AD risk?

We cannot say, but it is an interesting question. We selected the four late-onset Alzheimer’s risk genes (APOE, CD2AP, CLU, SORL1) based on human genetics data and brain expression in zebrafish larvae, not based on their likelihood to modify sleep behaviour, which we could have tried by searching for overlaps with GWAS of sleep phenotypes, for example. Consequently, we find it remarkable that all four of these genes caused a night-time sleep phenotype when mutated. We also find it reassuring that knockout of appa/appb and psen2 did not cause a night-time sleep phenotype, which largely excludes the possibility that the phenotype is a technical artefact (e.g. caused by the F0 knockout method) or a property of every gene expressed in the larval brain.

Having said that, it could still be a coincidence, rather than a special property of genes associated with late-onset AD. In addition to testing additional late-onset Alzheimer’s risk genes, the ideal way to answer this question would be to test in parallel a random set of genes expressed in the brain at this stage of development. From this random set, one could estimate the proportion of genes that cause a night-time sleep phenotype when mutated. One could then use that information to test whether late-onset Alzheimer’s risk genes are indeed enriched for genes that cause a night-time sleep phenotype when mutated.

For those mutants that cause night-time sleep disturbances, do these phenotypes share a common underlying pathway? e.g. Do 5-HT reuptake inhibitors promote sleep across all 4 late-onset genes in addition to psen1? Can 5-HT reuptake inhibitors reverse other AD-related pathologies in zebrafish? Can compounds be identified that have a common behavioral fingerprint across all or multiple AD risk genes? Do these modify sleep phenotypes?

To attempt to answer these questions, we used ZOLTAR to generate predictions for all the knockout behavioural fingerprints presented in the study, in the same way as for sorl1 in Fig. 5 and Fig. 5–supplement 1. Here are the indications, targets, and KEGG pathways which are shared by the largest number of knockouts (Author response image 1):

– One indication is shared by 4/7 knockouts: “opioid dependence” (significant for appa/appb, psen1, apoea/apoeb, cd2ap).

– Four targets are shared by 4/7 knockouts: “strychnine-binding glycine receptor” (psen1, apoea/apoeb, clu, sorl1); “neuronal acetylcholine receptor beta-2” (psen1, apoea/apoeb, cd2ap, clu); thyroid peroxidase (psen1, apoea/apoeb, cd2ap, clu); carbonic anhydrase IV (appa/appb, psen1, psen2, cd2ap).

– Three KEGG pathways are shared by 5/7 knockouts: “cholinergic synapse” (psen1, apoea/apoeb, cd2ap, clu, sorl1); tyrosine metabolism (psen2, apoea/apoeb, cd2ap, clu, sorl1); and “nitrogen metabolism” (appa/appb, psen1, psen2, apoea/apoeb, cd2ap).

As reminder, we hypothesised that loss of Sorl1 affected serotonin signalling based on the following annotations being significant: indication “depression”, target “serotonin transporter”, and KEGG pathway “serotonergic synapse”. Indication “depression” is only significant for sorl1 knockouts; target “serotonin transporter” is also significant for appa/appb and psen2 knockouts; and KEGG pathway “serotonergic synapse” is also significant for psen2 knockouts. ZOLTAR therefore does not predict serotonin signalling to be a major theme common to all mutants with a night-time sleep loss phenotype.

Particularly interesting is cholinergic signalling appearing in the most common targets and KEGG pathways. Acetylcholine signalling is a major theme in research on AD. For example, the first four drugs ever approved by the FDA to treat AD were acetylcholinesterase inhibitors, which increase acetylcholine signalling by preventing its breakdown by acetylcholinesterase. These drugs are generally considered only to treat symptoms and not modify disease course, but this view has been called into question (Munoz-Torrero, 2008; Relkin, 2007). If, as ZOLTAR suggests, mutations in several Alzheimer’s risk genes affect cholinergic signalling early in development, this would point to a potential causal role of cholinergic disruption in AD.

Author response image 1.

Common predictions from ZOLTAR for the seven Alzheimer’s risk genes tested. Predictions from ZOLTAR which are shared by multiple knockout behavioural fingerprints presented in the study. Only indications, targets, and KEGG pathways which are significant for at least three of the seven knockouts tested are shown, ranked from the annotations which are significant for the largest number of knockouts.

Finally, the web- based platform presented could be expanded to facilitate comparison of other behavioral phenotypes, including stimulus-evoked behaviors.

Yes, absolutely. The behavioural dataset we used (Rihel et al., 2010) did not measure other stimuli than day/night light transitions, but the “SauronX” platform and dataset (MyersTurnbull et al., 2022) seems particularly well suited for this. To provide some context, we and collaborators have occasionally used the dataset by Rihel et al. (2010) to generate hypotheses or find candidate drugs that reverse a behavioural phenotype measured in the sleep/wake assay (Ashlin et al., 2018; Hoffman et al., 2016). The present work was the occasion to enable a wider and more intuitive use of this dataset through the ZOLTAR app, which has already proven successful. Future versions of ZOLTAR may seek to incorporate larger drug datasets using more types of measurements.

Finally, the authors propose but do not test the hypothesis that sorl1 might regulate localization/surface expression of 5-HT2 receptors. This could provide exciting / more convincing mechanistic support for the assertion that serotonin signaling is disrupted upon loss of AD-associated genes.

While working on the Author Response, we made some changes to the analysis ran by ZOLTAR to calculate enrichments (see Methods and github.com/francoiskroll/ZOLTAR, notes on v2). With the new version, 5-HT receptor type 2 is not a significantly enriched target for the sorl1 knockout fingerprint but type 4 is. 5-HT receptor type 4 was also shown to interact with sorting nexin 27, a subunit of retromer, so is a promising candidate (Joubert et al., 2004). Antibodies against human 5-HT receptor type 2 and 4a exist; whether they would work in zebrafish remains to be tested. In our experience, the availability of antibodies suitable for immunohistochemistry in the zebrafish is a serious experimental roadblock.

Note, all the results presented in the “Version of Records” are from ZOLTAR v2.

Despite these important considerations, this study provides a valuable platform for highthroughput analysis of sleep phenotypes and correlation with small-molecule-induced sleep phenotypes.

Strengths:

- Provides a useful platform for comparison of sleep phenotypes across genotypes/drug manipulations.

- Presents convincing evidence that night-time sleep is disrupted in mutants for multiple late onset AD-related genes.

- Provides potential mechanistic insights for how AD-related genes might impact sleep and identifies a few drugs that modify their identified phenotypes

Weaknesses:

- Exploration of potential mechanisms for serotonin disruption in sorl1 mutants is limited.

- The pipeline developed can only be used to examine sleep-related / spontaneous movement phenotypes and stimulus-evoked behaviors are not examined.

- Comparisons between mutants/exploration of commonly affected pathways are limited.

Thank you for these excellent suggestions, please see our answers above.

Reviewer #2 (Public Review):

Summary:

This work delineates the larval zebrafish behavioral phenotypes caused by the F0 knockout of several important genes that increase the risk for Alzheimer's disease. Using behavioral pharmacology, comparing the behavioral fingerprint of previously assayed molecules to the newly generated knockout data, compounds were discovered that impacted larval movement in ways that suggest interaction with or recovery of disrupted mechanisms.

Strengths:

This is a well-written manuscript that uses newly developed analysis methods to present the findings in a clear, high-quality way. The addition of an extensive behavioral analysis pipeline is of value to the field of zebrafish neuroscience and will be particularly helpful for researchers who prefer the R programming language. Even the behavioral profiling of these AD risk genes, regardless of the pharmacology aspect, is an important contribution. The recovery of most behavioral parameters in the psen2 knockout with betamethasone, predicted by comparing fingerprints, is an exciting demonstration of the approach. The hypotheses generated by this work are important stepping stones to future studies uncovering the molecular basis of the proposed gene-drug interactions and discovering novel therapeutics to treat AD or co-occurring conditions such as sleep disturbance.

Weaknesses:

- The overarching concept of the work is that comparing behavioral fingerprints can align genes and molecules with similarly disrupted molecular pathways. While the recovery of the psen2 phenotypes by one molecule with the opposite phenotype is interesting, as are previous studies that show similar behaviorally-based recoveries, the underlying assumption that normalizing the larval movement normalizes the mechanism still lacks substantial support. There are many ways that a reduction in movement bouts could be returned to baseline that are unrelated to the root cause of the genetically driven phenotype. An ideal experiment would be to thoroughly characterize a mutant, such as by identifying a missing population of neurons, and use this approach to find a small molecule that rescues both behavior and the cellular phenotype. If the connection to serotonin in the sorl1 was more complete, for example, the overarching idea would be more compelling.

Thank you for this cogent criticism.

On the first point, we were careful not to claim that betamethasone normalises the molecular/cellular mechanism that causes the psen2 behavioural phenotype. Having said that, yes, to a certain extent that would be the hope of the approach. As you say, every compound which normalises the behavioural fingerprint will not normalise the underlying mechanism, but the opposite seems true: every compound that normalises the underlying mechanism should also normalise the behavioural fingerprint. We think this logic makes the “behaviour-first” approach innovative and interesting. The logic is to discover compounds that normalise the behavioural phenotype first, only subsequently test whether they also normalise the molecular mechanism, akin to testing first whether a drug resolves the symptoms before testing whether it actually modifies disease course. While in practice testing thousands of drugs in sufficient sample sizes and replicates on a mutant line is challenging, the dataset queried through ZOLTAR provides a potential shortcut by shortlisting in silico compounds that have the opposite effect on behaviour.

You mention a “reduction in movement bouts” but note here that the number of behavioural parameters tested is key to our argument. To take the two extremes, say the only behavioural parameter we measured in psen2 knockout larvae was time active during the day, then, yes, any stimulant used at the right concentration could probably normalise the phenotype. In this situation, claiming that the stimulant is likely to also normalise the underlying mechanism, or even that it is a genuine “phenotypic rescue”, would not be convincing. Conversely, say we were measuring thousands of behavioural parameters under various stimuli, such as swimming speed, position in the well, bout usage, tail movements, and eye angles, it seems almost impossible for a compound to rescue most parameters without also normalising the underlying mechanism. The present approach is somewhere inbetween: ZOLTAR uses six behavioural parameters for prediction (e.g. Fig 6a), but all 17 parameters calculated by FramebyFrame can be used to assess rescue during a subsequent experiment (Fig. 6c). For both, splitting each parameter in day and night increases the resolution of the approach, which partly answers your criticism. For example, betamethasone rescued the day-time hypoactivity without causing night-time hyperactivity, so we are not making the “straw man argument” explained above of using any broad stimulant to rescue the hypoactivity phenotype.

Furthermore, for diseases where the behavioural defect is the primary concern, such as autism or bipolar disorder, perhaps this behaviour-first approach is all that is needed, and whether or not the compound precisely rescues the underlying mechanism is somewhat secondary. The use of lithium to prevent manic episodes in bipolar disorder is a good example. It was initially tested because mania was thought to be caused by excess uric acid and lithium can dissolve uric acid (Mitchell and Hadzi-Pavlovic, 2000). The theory is now discredited, but lithium continues to be used without a precise understanding of its mode of action. In this example, behavioural rescue alone, assuming the secondary effects are tolerable, is sufficient to be beneficial to patients, and whether it modulates the correct causal pathway is secondary.

On the second point, we agree that testing first ZOLTAR on a mutant for which we have a fairly good understanding of the mechanism causing the behavioural phenotype could have been a productive approach. Note, however, that examples already exist in the literature (Ashlin et al., 2018; Hoffman et al., 2016). The example from Hoffman et al. (2016) is especially convincing. Drugs generating behavioural fingerprints that positively correlate with the cntnap2a/cntnap2b double knockout fingerprint were enriched with NMDA and GABA receptor antagonists. In experiments analogous to our citalopram and fluvoxamine treatments (Fig. 5c,d and Fig. 5–supplement 1c,d), cntnap2a/cntnap2b knockout larvae were overly sensitive to the NMDA receptor antagonist MK-801 and the GABAA receptor antagonist pentylenetetrazol (PTZ). Among other drugs tested, zolpidem, a GABAA receptor agonist, caused opposite effects on wild-type and cntnap2a/cntnap2b knockout larvae. Knockout larvae were found to have fewer GABAergic neurons in the forebrain. While these studies did not use precisely the same analysis that ZOLTAR runs, they used the same rationale and behavioural dataset to make these predictions (Rihel et al., 2010), which shows that approaches like ZOLTAR can point to causal processes.

On your last point, we hope our experiment testing fluvoxamine, another selective serotonin reuptake inhibitor (SSRI), makes the connection between Sorl1 and serotonin signalling more convincing.

- The behavioral difference between the sorl1 KO and scrambled at the higher dose of the citalopram is based on a small number of animals. The KO Euclidean distance measure is also more spread out than for the other datasets, and it looks like only five or so fish are driving the group difference. It also appears as though the numbers were also from two injection series. While there is nothing obviously wrong with the data, I would feel more comfortable if such a strong statement of a result from a relatively subtle phenotype were backed up by a higher N or a stable line. It is not impossible that the observed difference is an experimental fluke. If something obvious had emerged through the HCR, that would have also supported the conclusions. As it stands, if no more experiments are done to bolster the claim, the confidence in the strength of the link to serotonin should be reduced (possibly putting the entire section in the supplement and modifying the discussion). The discussion section about serotonin and AD is interesting, but I think that it is excessive without additional evidence.

We mostly agree with this criticism. One could interpret the larger spread of the data for sorl1 KO larvae treated with 10 µM citalopram as evidence that the knockout larvae do indeed react differently to the drug at this dose, regardless of being driven by a subset of the animals. The result indeed does not survive removing the top 5 (p = 0.87) or top 3 (p = 0.18) sorl1 KO + 10 µM larvae, but this amounts to excluding 20 (3/14) or 35 (5/14) % of the datapoints as potential outliers, which is unreasonable. In fact, excluding the top 5 sorl1 KO + 10 µM is equivalent to calling any datapoint with z-score > 0.2 an outlier (z-scores of the top 5 datapoints are 0.2–1.8). Applying consistently the same criterion to the scrambled + 10 µM group would remove the top 6 datapoints (z-scores = 0.5–3.9). Comparing the resulting two distributions again gives the sorl1 KO + 10 µM distribution as significantly higher (p = 0.0015). We would also mention that Euclidean distance, as a summary metric for distance between behavioural fingerprints, has limitations. For example, the measure will be more sensitive to changes in some parameters but not others, depending on how much room there is for a given parameter to change. We included this metric to lend support to the observation one can draw from the fingerprint plot (Fig. 5c) that sorl1 mutants respond in an exaggerated way to citalopram across many parameters, while being agnostic to which parameter might matter most.

Given that the HCR did not reveal anything striking, we agree with you that too much of our argument relied on this result being robust. As you and Reviewer #3 suggested, we repeated this experiment with a different SSRI, fluvoxamine (Fig. 5–supplement 1). We cannot readily explain why the result was opposite to what we found with citalopram, but in both cases sorl1 knockout larvae reacted differently than their control siblings, which adds an argument to our claim that ZOLTAR correctly predicted serotonin signalling as a disrupted pathway from the behavioural fingerprint. Accordingly, we mostly kept the Discussion on Sorl1 the same, although we concede that we may not have identified the molecular mechanism.

- The authors suggest two hypotheses for the behavioral difference between the sorl1 KO and scrambled at the higher dose of the citalopram. While the first is tested, and found to not be supported, the second is not tested at all ("Ruling out the first hypothesis, sorl1 knockouts may react excessively to a given spike in serotonin." and "Second, sorl1 knockouts may be overly sensitive to serotonin itself because post-synaptic neurons have higher levels of serotonin receptors."). Assuming that the finding is robust, there are probably other reasons why the mutants could have a different sensitivity to this molecule. However, if this particular one is going to be mentioned, it is surprising that it was not tested alongside the first hypothesis. This work could proceed without a complete explanation, but additional discussion of the possibilities would be helpful or why the second hypothesis was not tested.

There are no strong scientific reasons why this hypothesis was not tested. The lead author (F Kroll) moved to a different lab and country so the project was finalised at that time. We do not plan on testing this hypothesis at this stage. However, we adapted the wording to make it clear this is one possible alternative hypothesis which could be tested in the future. The small differences found by HCR are actually more in line with the new results from the fluvoxamine experiment, so it may also be that both hypotheses (pre-synaptic neurons releasing less serotonin when reuptake is blocked; or post-synaptic neurons being less sensitive) contribute. The fluvoxamine experiment was performed in a different lab (ICM, Paris; all other experiments were done in UCL, London) in a different wild-type strain (TL in ICM, AB x Tup LF in UCL), which complicates how one interprets this discrepancy.

- The authors claim that "all four genes produced a fairly consistent phenotype at night". While it is interesting that this result arose in the different lines, the second clutch for some genes did not replicate as well as others. I think the findings are compelling, regardless, but the sometimes missing replicability should be discussed. I wonder if the F0 strategy adds noise to the results and if clean null lines would yield stronger phenotypes. Please discuss this possibility, or others, in regard to the variability in some phenotypes.

For the first part of this point, please see below our answer to Reviewer #3, point (2) c.

Regarding the F0 strategy potentially adding variability, it is an interesting question which we tested in a larger dataset of behavioural recordings from F0 and stable knockouts for the same genes (unpublished). In summary, the F0 knockout method does not increase clutchto-clutch or larva-to-larva variability in the assay. F0 knockout experiments found many more significant parameters and larger effect sizes than stable knockout experiments, but this difference could largely be explained by the larger sample sizes of F0 knockout experiments. In fact, larger sample sizes within individual clutches appears to be a major advantage of the F0 knockout approach over in-cross of heterozygous knockout animals as it increases sensitivity of the assay without causing substantial variability. We plan to report in more detail on this analysis in a separate paper as we think it would dilute the focus of the present work.

- In this work, the knockout of appa/appb is included. While APP is a well-known risk gene, there is no clear justification for making a knockout model. It is well known that the upregulation of app is the driver of Alzheimer's, not downregulation. The authors even indicate an expectation that it could be similar to the other knockouts ("Moreover, the behavioural phenotypes of appa/appb and psen1 knockout larvae had little overlap while they presumably both resulted in the loss of Aβ." and "Comparing with early-onset genes, psen1 knockouts had similar night-time phenotypes, but loss of psen2 or appa/appb had no effect on night-time sleep."). There is no reason to expect similarity between appa/appb and psen1/2. I understand that the app knockouts could unveil interesting early neurodevelopmental roles, but the manuscript needs to be clarified that any findings could be the opposite of expectation in AD.

On “there is no reason to expect similarity […]”, we disagree. Knockout of appa/appb and knockout of psen1 will both result in loss of Aβ (appa/appb encode Aβ and psen1 cleaves Appa/Appb to release Aβ, cf. Fig. 3e). Consequently, a phenotype caused by the loss of Aβ, or possibly other Appa/Appb cleavage products, should logically be found in both appa/appb and psen1 knockouts.

On “it is well known that the upregulation of APP is the driver of Alzheimer’s, not downregulation”; we of course agree. Among others, the examples of Down syndrome, APP duplication (Sleegers et al., 2006), or mouse models overexpressing human APP show definitely that overexpression of APP is sufficient to cause AD. Having said that, we would not be so quick in dismissing APP knockout as potentially relevant to understanding of AD.

Loss of soluble Aβ due to aggregation could contribute to pathology (Espay et al., 2023). Without getting too much into this intricate debate, links between levels of Aβ and risk of disease are often counter-intuitive too. For example, out of 138 PSEN1 mutations screened in vitro, 104 reduced total Aβ production and 11 even seemingly abolished the production of both Aβ40 and Aβ42 (Sun et al., 2017). In short, loss of soluble Aβ occurs in both AD and in our appa/appb knockout larvae.

We added a sentence in Results (section psen2 knockouts […]) to briefly justify our appa/appb knockout approach. To be clear, we do not want to imply, for example, that the absence of a night-time sleep phenotype for appa/appb is contradictory to the body of literature showing links between Aβ and sleep, including in zebrafish (Özcan et al., 2020). As you say, our experiment tested loss of App, including Aβ, while the literature typically reports on overexpression of APP, as in APP/PSEN1-overexpressing mice (Jagirdar et al., 2021).

Reviewer #3 (Public Review):

In this manuscript by Kroll and colleagues, the authors describe combining behavioral pharmacology with sleep profiling to predict disease and potential treatment pathways at play in AD. AD is used here as a case study, but the approaches detailed can be used for other genetic screens related to normal or pathological states for which sleep/arousal is relevant. The data are for the most part convincing, although generally the phenotypes are relatively small and there are no major new mechanistic insights. Nonetheless, the approaches are certainly of broad interest and the data are comprehensive and detailed. A notable weakness is the introduction, which overly generalizes numerous concepts and fails to provide the necessary background to set the stage for the data.

Major points

(1) The authors should spend more time explaining what they see as the meaning of the large number of behavioral parameters assayed and specifically what they tell readers about the biology of the animal. Many are hard to understand--e.g. a "slope" parameter.

We agree that some parameters do not tell something intuitive about the biology of the animal. It would be easy to speculate. For example, the “activity slope” parameter may indicate how quickly the animal becomes tired over the course of the day. On the other hand, fractal dimension describes the “roughness/smoothness” of the larva’s activity trace (Fig. 2–supplement 1a); but it is not obvious how to translate this into information about the physiology of the animal. We do not see this as an issue though. While some parameters do provide intuitive information about the animal’s behaviour (e.g. sleep duration or sunset startle as a measure of startle response), the benefit of having a large number of behavioural parameters is to compare behavioural fingerprints and assess rescue of the behavioural phenotype by small molecules (Fig. 6c). For this purpose, the more parameters the better. The “MoSeq” approach from Wiltschko et al., 2020 is a good example from literature that inspired our own Fig. 6c. While some of the “behavioural syllables” may be intuitive (e.g. running or grooming), it is probably pointless to try to explain the ‘meaning’ of the “small left turn in place with head motion” syllable (Wiltschko et al., 2020). Nonetheless, this syllable was useful to assess whether a drug specifically treats the behavioural phenotype under study without causing too many side effects. Unfortunately, ZOLTAR has to reduce the FramebyFrame fingerprint (17 parameters) to just six parameters to compare it to the behavioural dataset from Rihel et al., 2010, but here, more parameters would almost certainly translate into better predictions too, regardless of their intuitiveness.

It is true however that we did not give much information on how some of the less intuitive parameters, such as activity slope or fractal dimension, are calculated or what they describe about the dataset (e.g. roughness/smoothness for fractal dimension). We added a few sentences in the legend of Fig. 2–supplement 1.

(2) Because in the end the authors did not screen that many lines, it would increase confidence in the phenotypes to provide more validation of KO specificity. Some suggestions include:

a. The authors cite a psen1 and psen2 germline mutant lines. Can these be tested in the FramebyFrame R analysis? Do they phenocopy F0 KO larvae?

We unfortunately do not have those lines. We investigated the availability of importing a psen2 knockout line from abroad, but the process of shipping live animals is becoming more and more cost and time prohibitive. However, we observed the same pigmentation phenotype for psen2 knockouts as reported by Jiang et al., 2018, which is at least a partial confirmation of phenocopying a loss of function stable mutant.  

b. psen2_KO is one of the larger centerpieces of the paper. The authors should present more compelling evidence that animals are truly functionally null. Without this, how do we interpret their phenotypes?

We disagree that there should be significant doubt about these mutants being truly functionally null, given the high mutation rate and presence of the expected pigmentation phenotype (Jiang et al., 2018, Fig. 3f and Fig. 3–supplement 3a). The psen2 F0 knockouts were virtually 100% mutated at three exons across the gene (mutation rates were locus 1: 100 ± 0%; locus 2: 99.99 ± 0.06%; locus 3: 99.85 ± 0.24%). Additionally, two of the three mutated exons had particularly high rates of frameshift mutations (locus 1: 97 ± 5%; locus 2: 88 ± 17% frameshift mutation rate). It is virtually impossible that a functional protein is translated given this burden of frameshift mutations. Phenotypically, in addition to the pigmentation defect, double psen1/psen2 F0 knockout larvae had curved tails, the same phenotype as caused by a high dose of the γ-secretase inhibitor DAPT (Yang et al., 2008). These double F0 knockouts were lethal, while knockout of psen1 or psen2 alone did not cause obvious morphological defects. Evidently, most larvae must have been psen2 null mutants in this experiment, otherwise functional Psen2 would have prevented early lethality.

Translation of zebrafish psen2 can start at downstream start codons if the first exon has a frameshift mutation, generating a seemingly functional Psen2 missing the N-terminus (Jiang et al., 2020). Zebrafish homozygous for this early frameshift mutation had normal pigmentation, showing it is a reliable marker of Psen2 function even when it is mutated. This mechanism is not a concern here as the alternative start codons are still upstream of two of the three mutated exons (the alternative start codons discovered by Jiang et al., 2020 are in exon 2 and 3, but we targeted exon 3, exon 4, and exon 6).

We understand that the zebrafish community may be cautious about F0 phenotyping compared to stably generated mutants. As mentioned to Reviewer #2, we are planning to assemble a paper that expressly compares behavioural phenotypes measured in F0 vs. stable mutants to allay some of these concerns. Our current manuscript, which combines CRISPR-Cas9 rapid F0 screening with in silico pharmacological predictions, inevitability represents a first step in characterizing the functions of these genes. 

c. Related to the above, for cd2AP and sorl1 KO, some of the effect sizes seem to be driven by one clutch and not the other. In other words, great clutch-to-clutch variability. Should the authors increase the number of clutches assayed?

Correct, there is substantial clutch-to-clutch variability in this behavioural assay. This is not specific to our experiments. Even within the same strain, wild-type larvae from different clutches (i.e. non-siblings) behave differently (Joo et al., 2021). This is why it is essential to compare behavioural phenotypes within individual clutches (i.e. from a single pair of parents, one male and one female), as we explain in Methods (section Behavioural video-tracking) and in the documentation of the FramebyFrame package. We often see two different experimental designs in literature: comparing non-sibling wild-type and mutant larvae, or pooling different clutches which include all genotypes (e.g. pooling multiple clutches from heterozygous in-crosses or pooling wild-type clutches before injecting them). The first experimental design causes false positive findings (Joo et al., 2021), as the clutchto-clutch variability we and others observe gets interpreted as a behavioural phenotype. The second experimental design should not cause false positives but likely decreases the sensitivity of the assay by increasing the spread within genotypes. In both cases, the clutch-to-clutch variability is hidden, either by interpreting it as a phenotype (first case) or by adding it to animal-to-animal variability (second case). Our experimental design is technically more challenging as it requires obtaining large clutches from unique pairs of parents. However, this approach is better as it clearly separates the different sources of variability (clutch-to-clutch or animal-to-animal). As for every experiment, yes, a larger number of replicates would be better, but we do not plan to assay additional clutches at this time. Our work heavily focuses on the sorl1 and psen2 knockout behavioural phenotypes. The key aspects of these phenotypes were effectively tested in four experiments (five to six clutches) as sorl1 knockout larvae were also tracked in the citalopram and fluvoxamine experiments (Fig. 5 and Fig. 5–supplement 1), and psen2 knockout larvae were also tracked in the small molecule rescue experiment (Fig. 6 and Fig. 6–supplement 1).

The psen2 behavioural phenotype replicated well across the six clutches tested (pairwise cosine similarities: 0.62 ± 0.15; Author response image 2a). 5/6 clutches were less active and initiating more sleep bouts during the day, as we claimed in Fig. 3.

In the citalopram experiment, the H₂O-treated sorl1 knockout fingerprint replicated fairly well the baseline recordings in Fig. 4, despite the smaller sample size (cos = 0.30 and 0.78; Author response image 2b, see “KO Fig. 5”). 5/6 of the significant parameters presented in Fig. 4–supplement 4 moved in the same direction, and knockout larvae were also hypoactive during the day but hyperactive at night. Note that two clutches were tracked on the same 96-well plate in this experiment. We calculated each larva’s z-score using the average of its control siblings, then we averaged all the z-scores to generate the fingerprint. The H₂O treated sorl1 knockout clutch from the fluvoxamine experiment did not replicate well the baseline recordings (cos = 0.08 and 0.11; Author response image 2b, see “KO Fig. 5–suppl. 1”). Knockout larvae were hypoactive during the day as expected, but behaviour at night was not as robustly affected. As mentioned above, knockouts were made in a different genetic background (TL, instead of AB x Tup LF used for all other experiments), which could explain the discrepancy.

We also took the opportunity to check whether our SSRI treatments replicated well the data from Rihel et al., 2010. For both citalopram (n = 3 fingerprints in the database) and fluvoxamine (n = 4 fingerprints in the database), replication was excellent (cos ≥ 0.67 for all comparisons of a fingerprint from this study vs. a fingerprint from Rihel et al. 2010; Author response image 2c,d). Note that the scrambled + 10 µM citalopram and + 10 µM fluvoxamine fingerprints correlate extremely well (cos = 0.92; can be seen in Author response image 2c,d), which was predicted by the small molecule screen dataset.

Author response image 2.

Replication of psen2 and sorl1 F0 knockout fingerprints and SSRI treatments from Rihel et al., 2010. a, (left) Every psen2 F0 knockout behavioural fingerprint generated in this study. Each dot represents the mean deviation from the same-clutch scrambled-injected mean for that parameter (z-score, mean ± SEM). From the experiments in Fig. 6, presented is the psen2 F0 knockout + H₂O fingerprints. The fingerprints in grey (“not shown”) are from a preliminary drug treatment experiment we did not include in the final study. These fingerprints are from psen2 F0 knockout larvae treated with 0.2% DMSO, normalised to scrambled-injected siblings also treated with 0.2% DMSO. (right) Pairwise cosine similarities (−1.0–1.0) for the fingerprints presented. b, Every sorl1 F0 knockout behavioural fingerprint, as in a). c, The scrambled-injected + citalopram (10 µM) fingerprints (grey) in comparison to the citalopram (10–15 µM) fingerprints from the Rihel et al., 2010 database (green). d, The scrambled-injected + fluvoxamine (10 µM) fingerprint (grey) in comparison to the fluvoxamine fingerprints from the Rihel et al., 2010 database (pink). In c) and d), the scrambled-injected fingerprints are from the experiments in Fig. 5 and Fig. 5–suppl. 1, but were converted here into the behavioural parameters used by Rihel et al., 2010 for comparison. Parameters: 1, average activity (sec active/min); 2, average waking activity (sec active/min, excluding inactive minutes); 3, total sleep (hr); 4, number of sleep bouts; 5, sleep bout length (min); 6, sleep latency (min until first sleep bout).

(3) The authors make the point that most of the AD risk genes are expressed in fish during development. Is there public data to comment on whether the genes of interest are expressed in mature/old fish as well? Just because the genes are expressed early does not at all mean that early- life dysfunction is related to future AD (though this could be the case, of course). Genes with exclusive developmental expression would be strong candidates for such an early-life role, however. I presume the case is made because sleep studies are mainly done in juvenile fish, but I think it is really a prejy minor point and such a strong claim does not even need to be made.

This is a fair criticism but we do not make this claim (“early-life dysfunction is related to future AD”) from expression alone. The reviewer is probably referring to the following quote:

“[…] most of these were expressed in the brain of 5–6-dpf zebrafish larvae, suggesting they play a role in early brain development or function,” which does not mention future risk of AD. We do suggest that these genes have a function in development. After all, every gene that plays a role in brain development must be expressed during development, so this wording seemed reasonable. Nevertheless, we adapted the wording to address this point and Reviewer #2’s complaint below. As noted, the primary goal was to check that the genes we selected were indeed expressed in zebrafish larvae before performing knockout experiments. Our discussion does raise the hypothesis that mutations in Alzheimer’s risk genes impact brain development and sleep early in life, but this argument primarily relies on our observation that knockout of late-onset Alzheimer’s risk genes causes sleep phenotypes in 7-day old zebrafish larvae and from previous work showing brain structural differences in children at high genetic risk of AD (Dean et al., 2014; Quiroz et al., 2015), not solely on gene expression early in life.

Please also see our answer to a similar point raised by Reviewer #2 below (cf. Author response image 7).

(4) A common quandary with defining sleep behaviorally is how to rectify sleep and activity changes that influence one another. With psen2 KOs, the authors describe reduced activity and increased sleep during the day. But how do we know if the reduced activity drives increased behavioral quiescence that is incorrectly defined as sleep? In instances where sleep is increased but activity during periods during wake are normal or elevated, this is not an issue. But here, the animals might very well be unhealthy, and less active, so naturally they stop moving more for prolonged periods, but the main conclusion is not sleep per se. This is an area where more experiments should be added if the authors do not wish to change/temper the conclusions they draw. Are psen2 KOs responsive to startling stimuli like controls when awake? Do they respond normally when quiescent? Great care must be taken in all models using inactivity as a proxy for sleep, and it can harm the field when there is no acknowledgment that overall health/activity changes could be a confound. Particularly worrisome is the betamethasone data in Figure 6, where activity and sleep are once again coordinately modified by the drug.

This is a fair criticism. We agree it is a concern, especially in the case of psen2 as we claim that day-time sleep is increased while zebrafish are diurnal. We do not rely heavily on the day-time inactivity being sleep (the ZOLTAR predictions or the small molecule rescue do not change whether the parameter is called sleep or inactivity), but our choice of labelling can fairly be challenged.

To address “are psen2 KO responsive to startling stimuli like controls when awake/when quiescent”, we looked at the larvae’s behaviour immediately after lights abruptly switched on in the mornings. Almost every larva, regardless of genotype, responded strongly to every lights-off transition during the experiment. Instead, we chose the lights-on transition for this analysis because it is a weaker startling stimulus for the larvae than the lights-off transition (Fig. 3–supplement 3), potentially exposing differences between genotypes or behavioural states (quiescent or awake). We defined a larva as having reacted to the lights switching on if it made a swimming bout during the second (25 frames) a er the lights-on transition. Across two clutches and two lights-on transitions, an average of 65% (range 52–73%) of all larvae reacted to the stimulus. psen2 knockout larvae were similarly likely, if not more likely, to respond (in average 69% responded, range 60–76%) than controls (60% average, range 44– 75%). When the lights switched on, about half of the larvae (39–51%) would have been classified as asleep according to the one-minute inactivity definition (i.e. the larva did not move in the minute preceding the lights transition). This allowed us to also compare behavioural states, as suggested by the reviewer. For three of the four light transitions, larvae which were awake when lights switched on were more likely to react than asleep larvae, but this difference was not striking (overall, awake larvae were only 1.1× more likely to react; Author response image 3). Awake psen2 knockout larvae were 1.1× (range 1.04–1.11×) more likely to react than awake control larvae, so, yes, psen2 knockout larvae respond normally when awake. Asleep psen2 knockout larvae were 1.4× (range 0.63–2.19×) more likely to react than asleep control larvae, so psen2 knockouts are also more or equally likely to react than control larvae when asleep. In summary, the overall health of psen2 knockouts did not seem to be a significant confound in the experiment. As the reviewer suggested, if psen2 knockout larvae were seriously unhealthy, they would not be as responsive as control larvae to a startling stimulus.

Author response image 3.

psen2 F0 knockouts react normally to lights switching on, indicating they are largely healthy. At each lights-on transition (9 AM), each larva was categorised as awake if it had moved in the preceding one minute or asleep if it had been inactive for at least one minute. Darker tiles represent larvae which performed a swimming bout during the second following lights-on; lighter tiles represent larvae which did not move during that second. The total count of each waffle plot was normalised to 25 so plots can be compared to each other. The real count is indicated in the corner of each plot. Data is from the baseline psen2 knockout trackings presented in Fig. 3 and Fig. 3–suppl. 2.

Next, we compared inactive period durations during the day between psen2 and control larvae. If psen2 knockout larvae indeed sleep more during the day compared to controls, we may predict inactive periods longer than one minute to increase disproportionately compared to the increase in shorter inactive periods. This broadly appeared to be the case, especially for one of the two clutches (Author response image 4). In clutch 1, inactive periods lasting 1–60 sec were equally frequent in both psen2 and control larvae (fold change 1.0× during both days), while inactive periods lasting 1–2 min were 1.5× (day 1) and 2.5× (day 2) more frequent in psen2 larvae compared to control larvae. In clutch 2, 1–60 sec inactive periods were also equally frequent in both psen2 and control larvae, while inactive periods lasting 1–2 min were 3.4× (day 1) and 1.5× (day 2) more frequent in psen2 larvae compared to control larvae. Therefore, psen2 knockouts disproportionately increased the frequency of inactive periods longer than one minute, suggesting they genuinely slept more during the day.

Author response image 4.

psen2 F0 knockouts increased preferentially the frequency of longer inactive bouts. For each day and clutch, we calculated the mean distribution of inactive bout lengths across larvae of same genotype (psen2 F0 knockout or scrambled-injected), then compared the frequency of inactive bouts of different lengths between the two genotypes. For example, in clutch 1 during day 2, 0.01% of the average scrambled-injected larva’s inactive bouts lasted 111–120 seconds (X axis 120 sec) while 0.05% of the average psen2 F0 knockout larva lasted this long, so the fold change was 5×. Inactive bouts lasting < 1 sec were excluded from the analysis. In clutch 2, day 1 plot, two datapoints fall outside the Y axis limit: 140 sec, Y = 32×; 170 sec, Y = 16×. Data is from the baseline psen2 knockout trackings presented in Fig. 3 and Fig. 3–suppl. 2.

Ultimately, this criticism seems challenging to definitely address experimentally. A possible approach could be to use a closed-loop system which, after one minute of inactivity, triggers a stimulus that is sufficient to startle an awake larva but not an asleep larva. If psen2 knockout larvae indeed sleep more during the day, the stimulus should usually not be sufficient to startle them. Nevertheless, we believe the two analyses presented here are consistent with psen2 knockout larvae genuinely sleeping more during the day, so we decided to keep this label. We agree with the reviewer that the one-minute inactivity definition has limitations, especially for day-time inactivity.

(5) The conclusions for the serotonin section are overstated. Behavioural pharmacology purports to predict a signaling pathway disrupted with sorl1 KO. But is it not just possible that the drug acts in parallel to the true disrupted pathway in these fish? There is no direct evidence for serotonin dysfunction - that conclusion is based on response to the drug. Moreover, it is just one drug - is the same phenotype present with another SSRI? Likewise, language should be toned down in the discussion, as this hypothesis is not "confirmed" by the results (consider "supported"). The lack of measured serotonin differences further raises concern that this is not the true pathway. This is another major point that deserves further experimental evidence, because without it, the entire approach (behavioral pharm screen) seems more shaky as a way to identify mechanisms. There are any number of testable hypotheses to pursue such as a) Using transient transgenesis to visualize 5HT neuron morphology (is development perturbed: cell number, neurite morphology, synapse formation); b) Using transgenic Ca reporters to assay 5HT neuron activity.

Regarding the comment, “is it not just possible that the drug acts in parallel to the true disrupted pathway”, we think no, assuming we understand correctly the question. Key to our argument is the fact that sorl1 knockout larvae react differently to the drug(s) than control larvae. As an example, take night-time sleep bout length, which was not affected by knockout of sorl1 (Fig. 4–supplement 4). For the sake of the argument, say only dopamine signalling (the “true disrupted pathway”) was affected in sorl1 knockouts and that serotonin signalling was intact. Assuming that citalopram specifically alters serotonin signalling, then treatment should cause the same increase in sleep bout length in both knockouts and controls as serotonin signalling is intact in both. This is not what we see, however. Citalopram caused a greater increase in sleep bout length in sorl1 knockouts than in scrambled-injected larvae. In other words, the effect is non-additive, in the sense that citalopram did not add the same number of z-scores to sorl1 knockouts or controls. We think this shows that serotonin signalling is somehow different in sorl1 knockouts. Nonetheless, we concede that the experiment does not necessarily say much about the importance of the serotonin disruption caused by loss of Sorl1. It could be, for example, that the most salient consequence of loss of Sorl1 is cholinergic disruption (see reply to Reviewer #1 above) and that serotonin signalling is a minor theme.

Furthermore, we agree with the reviewer and Reviewer #2 that the conclusions were overly confident. As suggested, we decided to repeat this experiment with another SSRI, fluvoxamine. Please find the results of this experiment in Fig. 5–supplement 1. The suggestions to further test the serotonin system in the sorl1 knockouts are excellent as well, however we do not plan to pursue them at this stage.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Major Comments:

- Data are presented in a variety of different ways, occasionally making comparisons across figures difficult. Perhaps at a minimum, behavioral fingerprints as in Figure 3 - Supplementary Figure 1 should be presented for all mutants in the main figures.

We like this suggestion! Thank you. We brought the behavioural fingerprints figure (previously Fig. 4–supplement 5) as main Fig. 4, and put the figure focused on the sorl1 knockout behavioural phenotype in supplementary, with the other gene-by-gene figures.

- It is not clear why some data were selected for supplemental rather than main figures. In many cases, detailed phenotypic data is provided for one example mutant in the main figures, and then additional mutants are described in detail in the supplement. Again, to facilitate comparisons between mutants, fingerprints could be provided for all mutants in a main figure, with detailed analyses moved to the supplements.

The logic was to dedicate one main figure to psen2 (Fig. 3) as an example of an early-onset Alzheimer’s risk gene, and one to sorl1 (previously Fig. 4) as an example of a late-onset Alzheimer’s risk gene. We focused on them in main figures as they are both tested again later (Fig. 5 and Fig. 6). Having said that, we agree that the fingerprints may be a better use of main figure space than the parameters plots. In addition to the above (fingerprints of lateonset Alzheimer’s risk genes in main figure), we rearranged the figures in the early-onset AD section to have the psen2 F0 knockout fingerprint in main.

- The explication of the utility of behavioral fingerprinting on page 35 is somewhat confusing. The authors describe drugs used to treat depression as enriched among small molecules anti-correlating with the sorl1 fingerprint. However, in Figure 5 - Supplementary Figure 1, drugs used to treat depression are biased toward positive cosines, which are indicated as having a more similar fingerprint to sorl1. These drugs should be described as more present among compounds positively correlating with the sorl1 fingerprint.

Sorry, the confusion is about “(anti-)correlating”. Precisely, we meant “correlating and/or anti-correlating”, not just anti-correlating. We changed to that wording. In short, the analysis is by design agnostic to whether compounds with a given annotation are found more on the positive cosines side (le side in Fig. 5–supplement 1a) or the negative cosines side (right side). This is because the dataset often includes both agonists and antagonists to a given pathway but these are difficult to annotate. For example, say 10 compounds in the dataset target the dopamine D4 receptor, but these are an unknown mix of agonists and antagonists. In this case, we want ZOLTAR to generate a low p-value when all 10 compounds are found at extreme ends of the list, regardless of which end(s) that is (e.g. top 8 and bottom 2 should give an extremely low p-value). Initially, we were splitting the list, for each annotation, into positive-cosine fingerprints and negative-cosine fingerprints and testing enrichment on both separately, but we think the current approach is better as it reflects better the cases we want to detect and considers all available examples for a given annotation in one test. In sum, yes, in this case drugs used to treat depression were mostly in the positive-cosine side, but the other drugs on the negative-cosine side also contributed to what the p-value is, so it reflects better the analysis to say “correlating and/or anticorrelating”. You can read more about our logic for the analysis in Methods (section Behavioural pharmacology from sorl1 F0 knockout’s fingerprint).

- The authors conclude the above-described section by stating: "sorl1 knockout larvae behaved similarly to larvae treated with small molecules targeting serotonin signaling, suggesting that the loss of Sorl1 disrupted serotonin signaling." Directionality here may be important. Are all of the drugs targeting the serotonin transporter SSRIs or similar? If so, then a correct statement would be that loss of Sorl1 causes similar phenotypes to drugs enhancing serotonin signaling. Finally, based on the correlation between serotonin transporter inhibitor trazodone and the sorl1 crispant phenotype, it is potentially surprising that the SSRI citalopram caused the opposite phenotype from sorl1, that is, increased sleep during the day and night. It is potentially interesting that this result was enhanced in mutants, and suggests dysfunction of serotonin signaling, but the statement that "our behavioral pharmacology approach correctly predicted from behaviour alone that serotonin signaling was disrupted" is too strong a conclusion.

We understand “disrupt” as potentially going either way, but this may not be the common usage. We changed to “altered”.

The point regarding directionality is excellent, however. We tested the proportion of serotonin transporter agonists and antagonists (SSRIs) on each side of the ranked list of small molecule fingerprints. We used the STITCH database for this analysis as it has more drug–target interactions, but likely less curated, than the Therapeutic Target Database (Szklarczyk et al., 2016). As with the Therapeutic Target Database, most fingerprints of compounds interacting with the serotonin transporter SLC6A4 were found on the side of positive cosines (p ~ 0.005 using the custom permutation test), which replicates Fig. 5a with a different source for the drug–target annotations (Author response image 5). On the side of positive cosines (small molecules which generate behavioural fingerprints correlating with the sorl1 fingerprint), there were 2 agonists and 26 antagonists. On the side of negative cosines (small molecules which generate behavioural fingerprints anti-correlating with the sorl1 fingerprint), there were 3 agonists and 2 antagonists. Using a Chi-squared test, this suggests a significant (p = 0.002) over-representation of antagonists (SSRIs) on the positive side (expected count = 24, vs. 26 observed) and agonists on the negative side (expected count = 1, vs. 3 observed). If SLC6A4 antagonists, i.e. SSRIs, indeed tend to cause a similar behavioural phenotype than knockout of sorl1, this would point in the direction of our original interpretation of the citalopram experiment; which was that excessive serotonin signalling is what causes the sorl1 behavioural phenotype.

Author response image 5.

Using the STITCH database as source of annotations also predicts SLC6A4 as an enriched target for the sorl1 behavioural fingerprint. Same figures as Fig. 5a,b but using the STITCH database (Szklarczyk et al., 2016) as source for the drug targets. a, Compounds annotated by STITCH as interacting with the serotonin transporter SLC6A4 tend to generate behavioural phenotypes similar to the sorl1 F0 knockout fingerprint. 40,522 compound–target protein pairs (vertical bars; 1,592 unique compounds) are ranked from the fingerprint with the most positive cosine to the fingerprint with the most negative cosine in comparison with the mean sorl1 F0 knockout fingerprint. Fingerprints of drugs that interact with SLC6A4 are coloured in yellow. Simulated p-value = 0.005 for enrichment of drugs interacting with SLC6A4 at the top (positive cosine) and/or bottom (negative cosine) of the ranked list by a custom permutation test. b, Result of the permutation test for top and/or bottom enrichment of drugs interacting with SLC6A4 in the ranked list. The absolute cosines of the fingerprints of drugs interacting with SLC6A4 (n = 52, one fingerprint per compound) were summed, giving sum of cosines = 15.9. To simulate a null distribution, 52 fingerprints were randomly drawn 100,000 times, generating a distribution of 100,000 random sum of cosines. Here, only 499 random draws gave a larger sum of cosines, so the simulated p-value was p = 499/100,000 = 0.005 **.

If this were true, we would expect, as the reviewer suggested, SSRI treatment (citalopram or fluvoxamine) on control larvae to give a similar behavioural phenotype as knockout of sorl1. However, this generally did not appear to be the case (sorl1 knockout fingerprint vs. SSRI-treated control fingerprint, cosine = 0.08 ± 0.35; Author response image 6).

Author response image 6.

sorl1 F0 knockouts in comparison to controls treated with SSRIs. a, sorl1 F0 knockout fingerprints (baseline recordings and sorl1 + H₂O fingerprint from the citalopram experiment) in comparison with the scrambled-injected + citalopram (1 or 10 µM) fingerprints. Each dot represents the mean deviation from the same-clutch scrambled-injected H₂O-treated mean for that parameter (z-score, mean ± SEM). b, As in a), sorl1 F0 knockout fingerprints (baseline recordings and sorl1 + H₂O fingerprint from the fluvoxamine experiment) in comparison with the scrambled-injected + fluvoxamine (10 µM) fingerprint.

The comparison with trazodone is an interesting observation, but it is only a weak serotonin reuptake inhibitor (Ki for SLC6A4 = 690 nM, vs. 8.9 nM for citalopram; Owens et al., 1997) and it has many other targets, both as agonist or antagonist, including serotonin, adrenergic, and histamine receptors (Mijur, 2011). In any case, the average trazodone fingerprint does not correlate particularly well to the sorl1 knockout fingerprint (cos = 0.3). Finally, the sorl1 knockout behavioural phenotype could be primarily caused by altered serotonin signalling in the hypothalamus, where we found both the biggest difference in tph1a/1b/2 HCR signal intensity (Fig. 5f) and the highest expression of sorl1 across scRNA-seq clusters (Fig. 1– supplement 2). In this case, it would be correct to expect sorl1 knockouts to react differently to SSRIs than controls, but it would be incorrect to expect SSRI treatment to cause the same behavioural phenotype, as it concurrently affects every other serotonergic neuron in the brain.

Finally, we agree the quoted conclusion was too strong given the current evidence. We since tested another SSRI, fluvoxamine, on sorl1 knockouts.

- Also in reference to Figure 5: in panel c, data are presented as deviation from vehicle treated. Because of this data presentation choice, it's no longer possible to determine whether, in this experiment, sorl1 crispants sleep less at night relative to their siblings. Does citalopram rescue / reverse sleep deficits in sorl1 mutants?

On your first point, please see our response to Reviewer #3 (2)c and Author Response 2b above.

On “does citalopram rescue/reverse sleep deficits in sorl1 mutants”: citalopram (and fluvoxamine) tends to reverse the key aspects of the sorl1 knockout behavioural phenotype by reducing night-time activity (% time active and total Δ pixels), increasing night-time sleep, and shortening sleep latency (Author response image 7). Extrapolating from the hypothesis presented in Discussion, this may be interpreted as a hint that sorl1 knockouts have reduced levels of 5-HT receptors, as increasing serotonin signalling using an SSRI tends to rescue the phenotype. However, we do not think that focusing on the significant behavioural parameters necessarily make sense here. Rather, one should take all parameters into account to conclude whether knockouts react differently to the drug than wild types (also see answer to Reviewer #3, (7) on this). For example, citalopram increased more the night-time sleep bout length of sorl1 knockouts than the one of controls (Fig. 5), but this parameter was not modified by knockout of sorl1 (Fig. 4). To explain the rationale more informally, citalopram is only used as a tool here to probe serotonin signalling in sorl1 knockouts, whether it worsens or rescues the behavioural phenotype is somewhat secondary, the key question is whether knockouts react differently than controls.

Author response image 7.

Comparing untreated sorl1 F0 knockouts vs. treated with SSRIs. a, sorl1 F0 knockout fingerprints (baseline recordings and sorl1 + H₂O fingerprint from the citalopram experiment) in comparison with the sorl1 knockout + citalopram (1 or 10 µM) fingerprints. Each dot represents the mean deviation from the same-clutch scrambled-injected H₂O-treated mean for that parameter (z-score, mean ± SEM). b, As in a), sorl1 F0 knockout fingerprints (baseline recordings and sorl1 + H₂O fingerprint from the fluvoxamine experiment) in comparison with the sorl1 + fluvoxamine (10 µM) fingerprint.

- Possible molecular pathways targeted by tinidazole, fenoprofen, and betamethasone are not described.

Tinidazole is an antibiotic, fenoprofen is a non-steroidal anti-inflammatory drug (NSAIDs), betamethasone is a steroidal anti-inflammatory drug. Interestingly, long-term use of NSAIDs reduces the risk of AD (in ’t Veld Bas A. et al., 2001). Several mechanisms are possible (Weggen et al., 2007), including reduction of Aβ42 production by interacting with γ-secretase (Eriksen et al., 2003). However, we did not explore the mechanism of action of these drugs on psen2 knockouts so do not feel comfortable speculating. We do not know, for example, whether these findings apply to betamethasone.

Minor Comments:

- On page 25, panel "g" should be labeled as "f".

Thank you!

- On page 35, a reference should be provided for the statement "From genomic studies of AD, we know that mutations in genes such as SORL1 modify risk by disrupting some biological processes.".

Thank you, this is now corrected. There were the same studies as mentioned in Introduction.

- On page 43, the word "and" should be added - "in wild-type rats and mice, overexpressing mutated human APP and PSEN1, AND restricting sleep for 21 days...".

Right, this sentence could be misread, we edited it. “overexpressing […]” only applied to the mice, not the rats (as they are wild-type); and both are sleep-deprived.

- On page 45, a reference should be provided for the statement "SSRIs can generally be used continuously with no adverse effects" and this statement should potentially be softened.

The reference is at the end of that sentence (Cirrito et al., 2011). You are correct though; we reformulated this statement to: “SSRIs can generally be used safely for many years”. SSRIs indeed have side effects.

- On page 54, a 60-minute rolling average is described as 45k rows, but this seems to be a 30-minute rolling average.

Thank you! We corrected. It should have been 90k rows, as in: 25 frames-per-second × 60 seconds × 60 minutes.

Reviewer #2 (Recommendations For The Authors):

"As we observed in the scRNA-seq data, most genes tested (appa, appb, psen1, psen2, apoea, cd2ap, sorl1) were broadly expressed throughout the 6-dpf brain (Fig. 1d and Fig. 1supplement 3 and 4)."

- apoea and appb are actually not expressed highly in the scRNA-seq data, and the apoea in situ looks odd, as if it has no expression. The appb gene mysteriously does not look as though it has high expression in the Raj data, but it is clearly expressed based on the in situ. I had previously noticed the same discrepancy, and I attribute it to the transcriptome used to map the Raj data, as the new DanioCell data uses a new transcriptome and indicates high appb expression in the brain. Please point out the discrepancy and possible explanation, perhaps in the figure legend.

All excellent points, thank you. We included them directly in Results text.

"most of these were expressed in the brain of 5-6-dpf zebrafish larvae, suggesting they play a role in early brain development or function."

- Evidence of expression does not suggest function, particularly not a function in brain development. As one example, almost half of the genome is expressed prior to the maternal-zygotic transition but does not have a function in those earliest stages of development. There are numerous other instances where expression does not equal function. Please change the sentence even as simply as "it is possible that they".

We mostly agree and edited to “[…], so they could play a role […]”.

Out of curiosity, we plotted, for each zebrafish developmental stage, the proportion of Alzheimer’s risk gene orthologues expressed in comparison to the proportion of all genes expressed (Author response image 8). We defined “all genes” as every gene that is expressed in at least one of the developmental stages (n = 24,856), not the complete transcriptome, to avoid including genes that are never expressed in the brain or whose expression is always below detection limit. We counted a gene as “expressed” if at least three cells had detectable transcripts. Using these definitions, 82 ± 7% of genes are expressed during development. For every developmental stage except 5 dpf (so 11/12), a larger proportion of Alzheimer’s risk genes than all genes are expressed (+5 ± 4%).

Author response image 8.

Proportion of Alzheimer’s risk genes orthologues expressed throughout zebrafish development. Proportion of Alzheimer’s risk genes orthologues (n = 42) and all genes (n = 24,856) expressed in the zebrafish brain at each developmental stage, from 12 hours post-fertilisation (hpf) to 15 days post-fertilisation (dpf). “All genes” corresponds to every gene expressed in the brain at any of the developmental stages, not the complete transcriptome. A gene is considered “expressed” (green) if at least three cells had detectable transcripts. Single-cell RNA-seq dataset from Raj et al., 2020.

"This frame-by-frame analysis has several advantages over previous methods that analysed activity data at the one-minute resolution."

- Which methods are these? There are no citations. There are certainly existing methods in the zebrafish field that can produce similar data to the method developed for this project. This new package is useful, as most existing software is not written in R, so it would help scientists who prefer this programming language. However, I would be careful not to oversell its novelty, since many methods do exist that produce similar results.

We added the references. There were referenced above after “we combined previous sleep/wake analysis methods”, but should have been referenced again here.

We are not convinced by this criticism. We would obviously not claim that the FramebyFrame package is as sophisticated and versatile as video-tracking tools like SLEAP or DeepLabCut, but we do think it answers a genuine need that was not addressed by other methods. Specifically, we know of many labs recording pixel count data across multiple days using the Zebrabox or DanioVision (we added support for DanioVision data after submission), but there were no packages to extract behavioural parameters from these data. Other methods involved standalone scripts with no documentation or version tracking. We would concede the FramebyFrame package is mostly targeted at these labs, but we already know of six labs routinely using it and were recently contacted by a researcher tracking Daphnia in the Zebrabox.

"F0 knockouts of both cutches" - "clutches"

Thank you!

Reviewer #3 (Recommendations For The Authors):

I would suggest totally revamping the Introduction section, and being sure to provide readers with the context and background they need for the data that comes thereafter. Key areas to touch on, in no particular order, include:

• Far more detail on the behavioral pharm screen upon which this paper builds, as a brief overview of that approach and the data generated are needed.

Thank you for the suggestion, we added a sentence hinting at this work in the last Introduction paragraph.

• Limitations of current zebrafish sleep/arousal assays that motivated the authors to develop a new, temporally high-resolution system.

We think this is better explained in Results, as is currently. For example, we need to point to Fig. 2–supplement 2a,b,c to explain that one-minute methods were missing sleep bouts and how FramebyFrame resolves this issue.

• A paragraph about sleep and AD, that does a better job of citing work in humans, mammalian, and invertebrate models that motivate the interest in the connection pursued here.

Sorry, we think this would place too much focus on sleep and AD. We want the main topic of the paper to be the behavioural pharmacology approach, not AD or sleep per se. As the Introduction states, we see Alzheimer’s risk genes as a case study for the behavioural pharmacology approach, rather than the reason why the approach was developed. Additionally, presenting sleep and AD in Introduction risks sounding like ZOLTAR is specifically designed for this context, while we conceived of it as much more generalisable and explicitly encourage its use to study genes associated to other diseases. Note that the paragraph you suggest is, we think, mostly present in Discussion (section Disrupted sleep and serotonin signalling […]).

• I modestly suggest eliminating making such a strong case for a gene-first approach being the best way to understand disease. It is not a zero-sum game, and there is plenty to learn from proteomics, metabolomics, etc. I suspect nobody will argue with the authors saying they leveraged the strength of their system and focused on key AD genes of interest.

From your point below, we understand the following quote is the source of the issue: “For finding causal processes, studying the genome, rather than the transcriptome or epigenome, is advantageous because the chronology from genomic variant to disease is unambiguous […]”. We did not want to suggest it is a zero-sum game, but we now understand how it can be read this way. We adapted slightly the wording. What we want to do is highlight the causality argument as the advantage of the genomics approach. We feel we do not read this argument often enough, while it remains a ‘magic power’ of genomics. One essentially does not have to worry about causality when studying a pathogenic germline variant, while it is a constant concern when studying the transcriptome or epigenome (i.e. did the change in this transcript’s level cause disease, or vice-versa?). To take an example in the context of AD, arguments based on genomics (e.g. Down syndrome or APP duplication) are often the definite arbiters when debating the amyloid hypothesis, exactly because their causality cannot be doubted.

Minor comments

(1) The opening of the introduction is perhaps overly broad, spending an entire paragraph on genome vs transcriptome, etc and making the claim that a gene-first approach is the best path. It isn't zero-sum, and the authors could just get right into AD and study genes of interest. Similar issues occur throughout the manuscript, with sentences/paragraphs that are not necessarily needed.

Please see our answer to your previous point. On the introduction being overly broad, we perfectly agree it is broad, but related to your point about presenting sleep and AD in the Introduction, we wish to talk about finding causal processes from genomics findings using behavioural pharmacology. We purposefully present research on AD as one instance of this broader goal, not the primary topic of the paper.

Another example are these sentences, which could be totally removed as the following paragraph starts off making the same point much more succinctly. "From genomic studies of AD, we know that mutations in genes such as SORL1 modify risk by disrupting some biological processes. Presumably, the same processes are disrupted in zebrafish sorl1 knockouts, and some caused the behavioural alterations we observed. Can we now follow the thread backwards and predict some of the biological processes in which Sorl1 is involved based on the behavioural profile of sorl1 knockouts?"

Thanks for the suggestion, but we think these sentences are useful to place back this Results section in the context of the Introduction. Think of the paper as mainly about the behavioural pharmacology approach, not on Alzheimer’s risk genes. The function of the paragraph here is not simply to explain the method by which we decided to study sorl1; it is to reiterate the rationale behind the behavioural pharmacology approach so that the reader understands where this Results section fits in the overall structure.

(2) Related to the above, the authors use lecanemab as an example to support their approach, but there has been a great deal of controversy regarding this drug. I don't think such extensive justification is needed. This study uses AD risk genes as a case study in a newly developed behavioral pharm pipeline. A great deal of the rest of the intro seems to just fill space and could be more focused on the study at hand. Interestingly, a er gene selection, the next step in their pipeline is sleep/wake analysis yet nothing is covered about AD and sleep in the intro. Some justification of that approach (why focus on sleep/wake as a starting point for behavioral pharm rather than learning and memory?) would be a better use of intro space.

There has indeed been controversy about lecanemab, but even the harshest critiques of the amyloid hypothesis concede that it slows down cognitive decline (Espay et al., 2023). That is all that is needed to support our argument, which is that research on AD started primarily from genomics and thereby yielded a disease-modifying drug. The controversy seems mostly focused on whether this effect size is clinically significant, and we think we correctly represent this uncertainty (e.g. “antibodies against Aβ such as lecanemab show promise in slowing down disease progression” and “the beneficial effects from targeting Aβ aggregation currently remain modest”).

Your next point is entirely fair. We mostly answered it above. To explain further, the primary reason why we measured sleep/wake behaviour is to match the behavioural dataset from Rihel et al., 2010 so we can use it to make predictions, not to study sleep in the context of AD per se. Sure, perhaps learning and memory would have been interesting, but we do not know of any study testing thousands of small molecules on zebrafish larvae during a memory task. We understand it can be slightly confusing though, as we then spend a paragraph of Discussion on sleep as a causal process in AD, but we obviously need to discuss this topic given the findings. However, to reiterate, we purposefully designed FramebyFrame and ZOLTAR to be useful beyond studying sleep/wake behaviour. For example, FramebyFrame would not calculate 17 behavioural parameters if the only goal was to measure sleep. We now mention the Rihel et al., 2010 study in the Introduction as you suggested above (“Far more detail on the behavioral pharm screen […]”), as that is the real reason why sleep/wake behaviour was measured in the first place.

(3) Also related to the above, another more relevant point that could be talked about in the intro is the need for more refined approaches to analyze sleep in zebrafish, given the effort that went into the new analysis system described here. Again, I think the context for why the authors developed this system would be more meaningful than the current content.

Thank you, we think we answered this point above (especially below Limitations of current zebrafish sleep/arousal assays […]).

(4) GWAS can stand for Genome-wide associate studies (plural) so I do not think the extra "s" is needed (GWASs) .

Indeed, that seems to be the common usage. Thank you.

(5) AD candidate risk genes were determined from loci using "mainly statistic colocalization". Can the authors add a few more details about what was done and what the "mainly" caveat refers to?

“Mainly” simply refers to the fact that other methods were used by Schwartzentruber et al. (2021) to annotate the GWAS loci with likely causal genes, but that most calls were ultimately made from statistic colocalisation. Readers can refer to this work to learn more about the methods used.

(6) The authors write "The loss of psen1 only had mild effects on behaviour" but I think they mean "sleep behaviors" as there could be many other behaviors that are disrupted but were not assessed. The same issue a few sentences later with "Behaviour during the day was not affected" and at the end of the following paragraph.

Yes, that would be more precise, thank you.

(7) For the Sorl1 pharmacology data, it is very hard to understand what is being measured behaviorally. Are the authors measuring sleep +/- citalopram, or something else, and why the change to Euclidean distance rather than all the measures we were just introduced to earlier in the manuscript?

We understand these plots (Fig. 5c,d) are less intuitive, but it is important that we show the difference in behaviour compared to H₂O-treated larvae of same genotype. The claim is that citalopram has a larger effect on knockouts than on controls, so the reader needs to focus on the effect of the drug on each genotype, not on the effect of sorl1 knockout. We added the standard fingerprints (i.e. setting controls to z-score = 0) here in Author response figures.

Euclidean distance takes as input all the measures we introduced. The point is precisely not to select a single measure. For example, say we were only plotting active bout number during the day, we would conclude that 10 µM citalopram has the same effect on knockouts and controls. Conversely, if we had taken sleep bout length at night, we would conclude 10 µM has a stronger effect on knockouts. What is the correct parameter to select? Using Euclidean distance resolves this by taking all parameters into account, rather than arbitrarily choosing one.

And what exactly is a "given spike in serotonin"? and how is this hypothesis the conclusion based on the lack of evidence for the second hypothesis? As the authors say, there could be other ways sorl1 knockouts are more sensitive to citalopram, so the absence of evidence for one hypothesis certainly does not support the other hypothesis.

We mean a given release of serotonin in the synaptic cleft. We have fixed this wording. 

We tend to disagree on the second point. We can think of two ways that sorl1 knockouts are more sensitive to citalopram: 1) they produce more serotonin, so blocking reuptake causes a larger spike in knockouts; or 2) blocking reuptake causes the same increase in both knockouts and wild-types but knockouts react more strongly to serotonin. We cannot in fact think of another way to explain the citalopram results. Not finding overwhelming evidence for 1) surely supports 2) somewhat, even if we do not have direct evidence for it. As an analogy, if two diagnoses are possible for a patient, testing negative for the first one supports the other one, even before it is directly tested.

(8) Again some language is used without enough care. Fish are referred to as "drowsier" under some drug conditions. How do the authors know the animal is drowsy? The phenotype is more specific - more sleep, less activity.

Thank you, we switched to “Furthermore, fenoprofen worsened the day-time hypoactivity of psen2 knockout larvae […]”.

(9) This sentence is misleading as it gives the impression that results in this manuscript suggest the conclusion: "Our observation that disruption of genes associated with AD diagnosis after 65 years reduces sleep in 7-day zebrafish larvae suggest that disrupted sleep may be a common mechanism through which these genes exert an effect on risk." That idea is widely held in the field, and numerous other previous manuscripts/reviews should be cited for clarity of where this hypothesis came from.

This idea is not widely held in the field. You likely read this point as “disrupted sleep is a risk factor for AD”, which, yes, is widely discussed in the field, but is not precisely what we are saying. We hypothesise that mutations in some of the Alzheimer’s risk genes cause disrupted sleep, possibly from a very early age, which then causes AD decades later. Studies and reviews on sleep and AD rarely make this hypothesis, at least not explicitly. The closest we know of are a few recent human genetics studies, typically using Mendelian Randomisation, finding that higher genetic risk of AD correlates with some sleep phenotypes, such as sleep duration (Chen et al., 2022; Leng et al., 2021). The work of Muto et al. (2021) is particularly interesting as it found correlations between higher genetic risk of AD and some sleep phenotypes in men in their early twenties, which seems unlikely to be a consequence of early pathology (Muto et al., 2021). Note, however, that even these studies do not mention sleep possibly being disrupted early in development, which is what our findings in zebrafish larvae support. As we mention, we think a team should test whether sleep is different in infants at higher genetic risk of AD, essentially performing an analogous, but obviously much more difficult, experiment as we did in zebrafish larvae. We do not know of any study testing this or even raising this idea, so evidently it is not widely held. Having said that, the studies we mention here were not referenced in the Discussion paragraph. We have now corrected this.

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Author response:

The following is the authors’ response to the original reviews

We would like to thank you and the reviewers for valuable feedback on the first version of the manuscript. We now addressed all of the issues raised by reviewers, mostly by implementing the suggested changes and clarifying important details in the revised version of the manuscript. A detailed response to each comment is provided in the rebuttal letter. Briefly, the main changes were as follow:

- We changed homeostatic balance to network balance especially when describing the main finding as the response changes induced by the stimulation occurred on a fast timescale. We speculate the sustained changes observed in the post-stimulation condition are the result of homeostatic mechanisms.

- We added additional verification on the target stimulation effect by adding a supplementary result showing its effect between the target and off-target z-planes, as well as demonstrating the minimal impact of the imaging laser to rsChRmine.

- We added a simple toy model illustrating suppression specifically applied to co-tuned cells that yields the response amplitude decrease, to further support our findings.

Public Reviews:

Reviewer #1 (Public review):

Summary:

Kang et al. provide the first experimental insights from holographic stimulation of auditory cortex. Using stimulation of functionally-defined ensembles, they test whether overactivation of a specific subpopulation biases simultaneous and subsequent sensory-evoked network activations.

Strengths:

The investigators use a novel technique to investigate the sensory response properties in functionally defined cell assemblies in auditory cortex. These data provide the first evidence of how acutely perturbing specific frequency-tuned neurons impacts the tuning across a broader population.

Weaknesses:

I have several main concerns about the interpretation of these data:<br /> (1) The premise of the paper suggests that sensory responses are noisy at the level of neurons, but that population activity is reliable and that different neurons may participate in sensory coding on different trials. However, no analysis related to single trial variance or overall stability of population coding is provided. Specifically, showing that population activity is stable across trials in terms of total activity level or in some latent low dimensional representation would be required to support the concept of "homeostatic balancing".

Thank you for raising an important point. We agree that the term ‘homeostatic balancing’ may be not the best term to be applied to explain the main results. We now have toned down on the homeostatic plasticity aspect to explain the main result. We have changed the term to a simple ‘network balance’, potentially due to various factors including rapid synaptic plasticity. We speculate the persistent activity of co-tuned cells in the post-stimulation session as a result of homeostatic balance, instead of rapidly changing back their responses to the baseline. Relevant changes are implemented throughout the manuscript including Introduction (e.g., lines 76-78) and Discussion sections (e.g., lines 453-456).

(2) Rebalancing would predict either that the responses of stimulated neurons would remain A) elevated after stimulation due to a hebbian mechanism or B) suppressed due to high activity levels on previous trials, a homeostatic mechanism. The authors report suppression in targeted neurons after stimulation blocks, but this appears similar to all other non-stimulated neurons. How do the authors interpret the post-stimulation effect in stimulated neurons?

It is true that the post stimulation effect of no response change both from co-tuned and non co-tuned neurons, and both from stimulation and control sessions. This could be due to neuronal activity being adapted and decreased enough from the consecutive presentation of acoustic stimuli themselves. However, we still think that if the stimulation driven co-tuned non stimulated neurons’ response decrease is highly driven by stimulation without homeostasis, at least their responses should bounce back during the post-stimulation. We agree that further investigation would be required to further confirm such effect. We elaborated this as another discussion point in the discussion section (lines 457-464).

(3) The authors suggest that ACtx is different from visual cortex in that neurons with different tuning properties are intermingled. While that is true at the level of individual neurons, there is global order, as demonstrated by the authors own widefield imaging data and others at the single cell level (e.g. Tischbirek et al. 2019). Generally, distance is dismissed as a variable in the paper, but this is not convincing. Work across multiple sensory systems, including the authors own work, has demonstrated that cortical neuron connectivity is not random but varies as a function of distance (e.g. Watkins et al. 2014). Better justification is needed for the spatial pattern of neurons that were chosen for stimulation. Further, analyses that account for center of mass of stimulation, rather than just the distance from any stimulated neuron would be important to any negative result related to distance.

Thank you for the further suggestion regarding the distance matter. While Watkins et al., 2014 and Levy and Reyes (2012) showed stronger connectivity for nearby cells as well as for more distant patches, on a functional level, Winkowski & Kanold 2013 showed high frequency heterogeneity especially in L2/3, where we targeted to image in this study. Thus, connected cells can have varied tuning consistent with spine imaging (Konnerth paper). We now also calculated the distance based on the center of mass of target cells to calculate the distance effect for an additional verification and still observed no distance related stimulation effect. We now replaced the Figure 4B with the result from the center of mass calculation.

(4) Data curation and presentation: Broadly, the way the data were curated and plotted makes it difficult to determine how well-supported the authors claims are. In terms of curation, the removal of outliers 3 standard deviations above the mean in the analysis of stimulation effects is questionable. Given the single-cell stimulation data presented in Figure 1, the reader is led to believe that holographic stimulation is quite specific. However, the justification for removing these outliers is that there may be direct stimulation 20-30 um from the target. Without plotting and considering the outliers as well, it is difficult to understand if these outsized responses are due to strong synaptic connections with neighboring neurons or rather just direct off-target stimulation. Relatedly, data presentation is limited to the mean + SEM for almost all main effects and pre-post stimulation effects are only compared indirectly. Whether stimulation effects are driven by just a few neurons that are particularly suppressed or distinct populations which are suppressed or enhanced remains unclear.

Thank you for pointing this out. Now we specifically removed neighboring cells that are < 20 um from the target point and we observed similar. We replaced all the relevant figures, texts, and statistical results to ensure that the exclusion was specific to overlapping neighboring cells.

Reviewer #2 (Public review):

The goal of HiJee Kang et al. in this study is to explore the interaction between assemblies of neurons with similar pure-tone selectivity in mouse auditory cortex. Using holographic optogenetic stimulation in a small subset of target cells selective for a given pure tone (PTsel), while optically monitoring calcium activity in surrounding non-target cells, they discovered a subtle rebalancing process: co-tuned neurons that are not optogenetically stimulated tend to reduce their activity. The cortical network reacts as if an increased response to PTsel in some tuned assemblies is immediately offset by a reduction in activity in the rest of the PTsel-tuned assemblies, leaving the overall response to PTsel unchanged. The authors show that this rebalancing process affects only the responses of neurons to PTsel, not to other pure tones. They also show that assemblies of neurons that are not selective for PTsel don't participate in the rebalancing process. They conclude that assemblies of neurons with similar pure-tone selectivity must interact in some way to organize this rebalancing process, and they suggest that mechanisms based on homeostatic signaling may play a role.

he conclusions of this paper are very interesting but some aspects of the study including methods for optogenetic stimulation, statistical analysis of the results and interpretation of the underlying mechanisms need to be clarified and extended.

(1) This study uses an all-optical approach to excite a restricted group of neurons chosen for their functional characteristics (their frequency tuning), and simultaneously record from the entire network observable in the FOV. As stated by the authors, this approach is applied for the first time to the auditory cortex, which is a tour de force. However, such an approach is complex and requires precise controls to be convincing. In the manuscript, several methodological aspects are not sufficiently described to allow a proper understanding.

(i) The use of CRmine together with GCaMP8s has been reported as problematic as the 2Ph excitation of GCaMP8s also excites the opsin. Here, the authors use a red-shifted version of CRmine to prevent such cross excitation by the imaging laser. To be convincing, they should explain how they controlled for the absence of rsCRmine activation by the 940nm light. Showing the fluorescence traces immediately after the onset of the imaging session would ensure that neurons are not excited as they are imaged.

Thank you for pointing this out. We realized that the important reference was omitted. Kishi et al. 2022 validated the efficacy of the rsChRmine compared to ChRmine. In this paper, they compared regular ChRmine and rsChRmine activity to different wavelengths and setting and showed the efficiency of rsChRmine with reduced optical cross talk. This reference is now included in the manuscript (line 98). We also checked the spontaneous baseline activity that lasted about 10 sec. before any of the sound presentation and observed a relatively stable activity throughout, rather than any imaging session onset related activation, which is also similar to what we see from another group of GCaMP6s transgenic animals.

Author response image 1.

Baseline fluorescence activity across cells within FOVs from AAV9-hSyn-GCaMP8s-T2A-rsChRmine injected mice (top) and CBA X Thy1-GCaMP6s F1 transgenic mice (bottom). Fluorescence levels and activity patterns remain similar, suggesting no evident imaging laser-induced activation from rsChRmine. Note that GCaMP8s examples are smoothed by using moving average of 4 points as GCaMP8s show faster activity.

(ii) Holographic patterns used to excite 5 cells simultaneously may be associated with out-of-focus laser hot spots. Cells located outside of the FOV could be activated, therefore engaging other cells than the targeted ones in the stimulation. This would be problematic in this study as their tuning may be unrelated to the tuning of the targeted cells. To control for such an effect, one could in principle decouple the imaging and the excitation planes, and check for the absence of out-of-focus unwanted excitation.

We further verified whether the laser power at the targeted z-plane influences cells’ activity at nearby z-planes. As the Reviewer pointed out, the previous x- and y-axis shifts were tested by single-cell stimulation. This time, we stimulated five cells simultaneously, to match the actual experiment setup and assess potential artifacts in other planes. We observed no stimulation-driven activity increase in cells at a z-planed shifted by 20 µm (Supplementary Figure 1). This confirms the holographic stimulation accurately manipulates the pre-selected target cells and the effects we observe is not likely due to out-of-focus stimulation artifacts. It is true that not all pre-selected cells showing significant response changes prior to the main experiment are effectively activated t every trial during the experiments. We varied the target cell distances across FOVs, from nearby cells to those farther apart within the FOV. We have not observed a significant relationship between the target cell distances and stimulation effect. Lastly, cells within < 20 µm of the target were excluded to prevent potential excitation due to the holographic stimulation power. Given the spontaneous movements of the FOV during imaging sessions due to animal’s movement, despite our efforts to minimize them, we believe that any excitation from these neighboring neurons would be directly from the stimulation rather than the light pattern artifact itself.

(iii) The control shown in Figure 1B is intended to demonstrate the precision of the optogenetic stimulation: when the stimulation spiral is played at a distance larger or equal to 20 µm from a cell, it does not activate it. However, in the rest of the study, the stimulation is applied with a holographic approach, targeting 5 cells simultaneously instead of just one. As the holographic pattern of light could produce out-of-focus hot spots (absent in the single cell control), we don't know what is the extent of the contamination from non-targeted cells in this case. This is important because it would determine an objective criterion to exclude non-targeted but excited cells (last paragraph of the Result section: "For the stimulation condition, we excluded non-target cells that were within 15 µm distance of the target cells...")

Highly sensitive neurons to certain frequency also shows the greatest adaptation effect, which can be observed the control condition. Therefore, the high sensitive neurons showing greater amplitude change is first related to the neuronal adaptation to its sensitive information. However, by stimulating the co-tuned target neurons, other co-tuned non-target neurons shows significantly greater amplitude decrease, compared to either non co-tuned target neurons stimulation or control (the latter did not meet the significance level).

We also tried putting more rigorous criterion as 20 um instead of 15 um as you pointed out since the spiral size was 20 um. The result yielded further significant response amplitude decrease due to the stimulation effect only from co-tuned non-target neurons for processing their preferred frequency information.

(2) A strength of this study comes from the design of the experimental protocol used to compare the activity in non-target co-tuned cells when the optogenetic stimulation is paired with their preferred tone versus a non-preferred pure tone. The difficulty lies in the co-occurrence of the rebalancing process and the adaptation to repeated auditory stimuli, especially when these auditory stimuli correspond to a cell's preferred pure tones. To distinguish between the two effects, the authors use a comparison with a control condition similar to the optogenetic stimulation conditions, except that the laser power is kept at 0 mW. The observed effect is shown as an extra reduction of activity in the condition with the optogenetic paired with the preferred tone, compared to the control condition. The specificity of this extra reduction when stimulation is synchronized with the preferred tone, but not with a non-preferred tone, is a potentially powerful result, as it points to an underlying mechanism that links the assemblies of cells that share the same preferred pure tones.

The evidence for this specificity is shown in Figure 3A and 3D. However, the universality of this specificity is challenged by the fact that it is observed for 16kHz preferring cells, but not so clearly for 54kHz preferring cells: these 54kHz preferring cells also significantly (p = 0.044) reduce their response to 54kHz in the optogenetic stimulation condition applied to 16kHz preferring target cells compared to the control condition. The proposed explanation for this is the presence of many cells with a broad frequency tuning, meaning that these cells could have been categorized as 54kHz preferring cells, while they also responded significantly to a 16kHz pure tone. To account for this, the authors divide each category of pure tone cells into three subgroups with low, medium and high frequency preferences. Following the previous reasoning, one would expect at least the "high" subgroups to show a strong and significant specificity for an additional reduction only if the optogenetic stimulation is targeted to a group of cells with the same preferred frequency. Figure 3D fails to show this. The extra reduction for the "high" subgroups is significant only when the condition of opto-stimulation synchronized with the preferred frequency is compared to the control condition, but not when it is compared to the condition of opto-stimulation synchronized with the non-preferred frequency.

Therefore, the claim that "these results indicate that the effect of holographic optogenetic stimulation depends not on the specific tuning of cells, but on the co-tuning between stimulated and non-stimulated neurons" (end of paragraph "Optogenetic holographic stimulation decreases activity in non-target co-tuned ensembles") seems somewhat exaggerated. Perhaps increasing the number of sessions in the 54kHz target cell optogenetic stimulation condition (12 FOV) to the number of sessions in the 16kHz target cell optogenetic stimulation condition (18 FOV) could help to reach significance levels consistent with this claim.

We previously also tested by randomly subselecting 12 FOVs from 16kHz stimulation condition to match the same number of FOV between two groups and did not really see any result difference. However, to further ensure the results, we now added three more dataset for 54 kHz target cell stimulation condition (now 15 FOV) which yielded similar outcome. We have now updated the statistical values from added datasets.

(3) To interpret the results of this study, the authors suggest that mechanisms based on homeostatic signaling could be important to allow the rebalancing of the activity of assemblies of co-tuned neurons. In particular, the authors try to rule out the possibility that inhibition plays a central role. Both mechanisms could produce effects on short timescales, making them potential candidates. The authors quantify the spatial distribution of the balanced non-targeted cells and show that they are not localized in the vicinity of the targeted cells. They conclude that local inhibition is unlikely to be responsible for the observed effect. This argument raises some questions. The method used to quantify spatial distribution calculates the minimum distance of a non-target cell to any target cell. If local inhibition is activated by the closest target cell, one would expect the decrease in activity to be stronger for non-target cells with a small minimum distance and to fade away for larger minimum distances. This is not what the authors observe (Figure 4B), so they reject inhibition as a plausible explanation. However, their quantification doesn't exclude the possibility that non-target cells in the minimum distance range could also be close and connected to the other 4 target cells, thus masking any inhibitory effect mediated by the closest target cell. In addition, the authors should provide a quantitative estimate of the range of local inhibition in layers 2/3 of the mouse auditory cortex to compare with the range of distances examined in this study (< 300 µm). Finally, the possibility that some target cells could be inhibitory cells themselves is considered unlikely by the authors, given the proportions of excitatory and inhibitory neurons in the upper cortical layers. On the other hand, it should be acknowledged that inhibitory cells are more electrically compact, making them easier to be activated optogenetically with low laser power.

Minimum distance is defined as the smallest distance non-target cell to any of the target cells. Thus, if this is local inhibition, it is likely that the closest target cell would have affected the non-target cells’ response changes. We also calculated the distance based on the center of mass of target cells to calculate the distance effect for an additional verification, based on both Reviewers’ comments, and still observed no distance related stimulation effect. The result is now updated in Figure 4B.

Based on previous literature, such as Levy & Reyes 2012, the excitatory and inhibitory connectivity is known to range around 100 um distance. Our results do not necessarily show any further effect observed for cells with distance below 100 um. This suggests that such effect is not limited to local inhibition. We also added further speculation on why our results are less likely due to increased inhibition, albeit the biological characteristics of inhibitory neurons to optogenetics.

Reviewer #3 (Public review):

Summary:

The authors optogenetically stimulate 5 neurons all preferring the same pure tone frequency (16 or 54 kHz) in the mouse auditory cortex using a holography-based single cell resolution optogenetics during sound presentation. They demonstrate that the response boosting of target neurons leads to a broad suppression of surrounding neurons, which is significantly more pronounced in neurons that have the same pure tone tuning as the target neurons. This effect is immediate and spans several hundred micrometers. This suggests that the auditory cortical network balances its activity in response to excess spikes, a phenomenon already seen in visual cortex.

Strengths:

The study is based on a technologically very solid approach based on single-cell resolution two-photon optogenetics. The authors demonstrate the potency and resolution of this approach. The inhibitory effects observed upon targeted stimulation are clear and the relative specificity to co-tuned neurons is statistically clear although the effect size is moderate.

Weaknesses:

The evaluation of the results is brief and some aspects of the observed homeostatic are not quantified. For example, it is unclear whether stimulation produces a net increase or decrease of population activity, or if the homeostatic phenomenon fully balances activity. A comparison of population activity for all imaged neurons with and without stimulation would be instructive. The selectivity for co-tuned neurons is significant but weak. Although it is difficult to evaluate this issue, this result may be trivial, as co-tuned neurons fire more strongly. Therefore, the net activity decrease is expected to be larger, in particular, for the number of non-co-tuned neurons which actually do not fire to the target sound. The net effect for the latter neurons will be zero just because they do not respond. The authors do not make a very strong case for a specific inhibition model in comparison to a broad and non-specific inhibitory effect. Complementary modeling work would be needed to fully establish this point.

Thank you for raising important points. We agree that the term homeostatic balancing may have been an overstatement. We toned down regarding the homeostatic plasticity and conclude the result from the rapid plasticity at a single trial level now. Regardless, the average activity level did not differ among stimulation conditions (control, 16kHz stim, and 54kHz stim), which seems to suggest that overall activity level has been maintained regardless of the stimulation. We added a new figure of the global activity change as Fig. 4A.

We also added a simple model work in which a suppression term was applied either to all neurons or specifically to non-target co-tuned cells to test our results from the data.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) For the first holography paper in A1, more information is needed about how holographic stimulation was performed and how stimulation artifacts were avoided or removed from the data set, especially as the text states that the PMTs were left open for the duration of the experiment.

We further clarified the rationale of leaving the shutter open to avoid any mechanic sounds to activate neurons in the AC. We further clarified that we keep the uncaging shutter open since the Bruker default setting (Software version: 5.7) opens and closes the shutter for the every iteration of the stimulation which generates extra heavy mechanical sounds which then hinders whether the activation is due to the sound or stimulation.

(2) The choice of the dF/F as the primary tool for quantifying data should be better justified. Presumably, cells have very different variances in baseline activity levels and baseline fluorescence levels that create a highly skewed distribution of responses across the population. Further, a

To take the baseline activity variances into account, we first calculate dF/F normalising to the baseline period (about 330 ms before the sound onset) right before each trial, per cell level. By doing so, we minimize any effect that could have been driven by variable baseline activity levels across neurons.

(3) More analysis should be performed to determine why 33% of stimulated cells are not activated, and instead are suppressed during stimulation. Is this related to a cells baseline fluorescence?

Great point. Although we tried our best to pre-select stimulation-responsive neurons before we start the actual experiments and head fix the animals as much as possible, these neurons do not stay as the “best stimulation-responsive neurons” throughout the entire imaging session. There can be various caveats on this. First, they seem to change their activity levels due to the optogenetic stimulation after they are exposed to acoustic stimulation. Second, since the AC is in the temporal side, it is likely to be more affected from the animals’ and their brain movements throughout the imaging session, which could be bigger than visual cortex or motor cortex. However, 33% of 5 cells is about 1.5 cells so it is usually missed about one cell on average, although some sessions have all 5 cells being stimulated while some other sessions have clearly less effective holographic stimulation effect.

We even manually visualised the fluorescence change due to the holographic stimulation before we start any imaging sessions. Regardless, they don’t stay as the ‘best stimulation responsive cells’ throughout which we cannot control the natural biological aspect of neuronal activities. Regardless, based on the significant stimulation effects observed by presenting different pure tone frequencies as well as delivering different target stimulation and no-stimulation control, we believe that the effect itself is valid. We added these caveats into the manuscript as a further discussion point and things to consider.

(4) The linear mixed-effects model should include time as a variable as A) the authors hypothesize that responses should be reduced over time due to sensory adaptation and that B) stimulation induced suppression might be dynamic (though they find it is not).

Since the stimulation effect seems to be independent from trial-by-trial changes among stimulation conditions (Fig. 4) and we now have toned down on the aspect of homeostasis, we kept the current mixed-effect model variables.

(5) More speculation is needed on why stimulation suppresses responses from the first trial onwards.

We further speculate such rapid response changes due to activity-dependent synaptic changes due to overall network energy shift from optogenetic stimulation to maintain the cortical circuit balance.  

(6) What does each dot represent in Figure 4a vs. Figure 4B? They are very different in number.

In 4A, each dot is average amplitude change values per each trial level. They are exactly same number of dots between frequency, cell groups and conditions as each dot represents each trial (20 each). The reason why it may look differ could be only due to some overlaps between frequencies.

In 4B, each dot is each cell. The reason why it’s denser in Stimulation conditions’ 16kHz preferring cells panel is that it naturally had more FOVs thus more cells to be plotted. We further clarified these details in the figure legend.

(7) How sensory responsive neurons were selected should be shown in the figures. Specifically, which fraction of the 30% of most responsive neurons were stimulated should be stated. Depending on the exact yield in the field of view, all or only a minority of strongly sensory responsive neurons are being stimulated, which in either case would color the interpretation of the data.

We tried varying the FOV as much as possible across sessions to ensure that FOVs are directly in the A1 covering a range of frequencies. If we cannot observe more than 80 neurons as sound responsive neurons from processed suite2p data, we searched for another FOV.  

We now included an example FOV of the widefield imaging we first conducted to identify A1, and another example FOV of the 2-photon imaging where we conducted a short sound presentation session to identify the sensory responsive neurons, as an inset of the ‘Cell selection’ part in Figure 1.

Reviewer #2 (Recommendations for the authors):

Minor points:

- p.4, last line: "of" probably missing "the processing the target..."

Fixed.

- p.5, top, end of the first paragraph of this page: Figure 3B and 3E don't show exemplar traces.

Corrected as Figure 2A and 2D.

- P.5, first sentence of the paragraph "Optogenetic holographic stimulation increases activity in targeted ensembles": reference to Figure 3A and 3D should rather be Figure 2A and 2D.

Corrected.

- P.9, 2nd paragraph: sentence with a strange syntax: "since their response amplitude..."

Corrected.

- Figure 2: panels C and F are missing.

Corrected.

- p.11, methods: "wasthen" should be "was then".

Corrected.

- p.12, analysis: it is not clearly explained why the sound evoked activity is computed based on the 160ms to 660ms after sound onset instead of 0ms to 660 ms. It is likely related to some potential contamination but it should be explicitly explained.

Due to the relatively slow calcium transient to more correctly capture the sound related evoked responses. Added this detail.

- Methods, analysis: the authors should better explain how they conducted the random permutation described in the Figures 1D, 2B and 2E. Which signals were permutated?

Random permutation to shuffle the target cell ID.

- References 55 and 56 don't explicitly state that excitatory neurons generally have stronger responses to sound than inhibitory neurons.

Thank you for pointing out this error. We replaced those references with Maor et al. 2016 and Kerlin et al. 2010, showing excitatory neurons show more selective tuning, and also changed the wording more appropriately.

- It is not explained whether the imaging sessions are performed on awake or anaesthetized animals. It is probably done on awake animals, but then it is not clear what procedure is used to get the animals used to the head restraint. It usually takes a few days for the mice to get used to it, and the stress level is often different at the beginning and end of an experiment. Given the experimental protocol used in the study, in which sessions are performed sequentially and compared to each other, this aspect could play a role. However, the main comparison made is probably safe as it compares a control condition (laser at 0mW) and conditions with optogenetic stimulation, all done with similar sequences of sessions.

The experiment was conducted on awake animals. Although we did not have any control on comparing their status in the beginning and the end of the experiment, they all had a widefield imaging session imaging session to identify the A1 region which uses the same head-fixation setup, thus they are more used to the setup when we conduct 2-photon imaging and stimulation. Regardless of the session, if animals show any sign of extra discomfort due to the unfamiliar setup, we keep them there for 10-15 minutes until they are accustomed to the setup with no movement. If they still show a sign of discomfort, we take them out and try for another day. We now included this detail on the manuscript.

Reviewer #3 (Recommendations for the authors):

- Evaluate the global effect of stimulation on the population activity averaged across all neurons (activated and non-activated).

Thank you for your suggestions. We now included a new Figure 3A that present the population activity across all responsive cells. The average activity level did not differ among stimulation conditions (control, 16kHz stim, and 54kHz stim).

- Evaluate with a simple model if a population of neurons with different sound tuning receiving non-specific inhibition would not produce the observed effect.

Thank you for the suggestion. We generated a simple model in which a suppression term was applied either to all neurons or specifically to non-target co-tuned cells to test our results from the data. We took a similar range of number of neurons and FOVs to closely simulate the model to the real dataset structure. On 50 simulated calcium traces of neurons (n),

Trace_n(t) = R_n(t) – theta_n + epsilon_n(t)

Where R_n(t) is a response amplitude from either baseline or stimulation session, theta_n is a suppression term applied either to all neurons or only to non-target co-tuned neurons, only during the stimulation session, and epsilon_n(t) is additive noise. Theta was defined based on the average amount of increased activity amplitudes generated from target neurons due to the stimulation, implemented from the real dataset with extra neuron-level jitter. Similar to the real data analyses, we compared the response change between the stimulation and baseline sessions’ trace amplitudes. By comparing two different model outcomes and the real data, we observed a significant effect of the model type (F(2, 2535) = 34.943, p < 0.0001) and interaction between the model type and cell groups was observed (F(2, 2535) = 36.348, p < 0.0001). Applying suppression to only non-target co-tuned cells during the stimulation session yielded a significant response amplitude decrease for co-tuned cells compared to non co-tuned cells (F(1, 2535) = 45.62, p < 0.0001), which resembles the real data In contrast, applying suppression to all non-target cells led to similar amplitude changes in both co-tuned and non co-tuned neurons (F(1, 2535) = 0.87, p = 0.35), which was not observed in either the real data or the simulated data restricted to co-tuned cell suppression. Therefore, the model predicts correctly that the specific suppression given to only co-tuned neurons drove the real data outcome. All of this information is now added into Methods and Results sections and the figure is added as Figure 3C.

Author response:

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

We have significant concerns about the eLife assessment and the reviews. The reviewers acknowledged substantial strengths in our work:

• Reviewer 3 noted that “the single-unit analyses of tuning direction are robustly characterized”, “the differences in neural correlations across behaviors, regions and perturbations are robust”, and “The evidence for these claims is solid.”

• Reviewer 2 stated that “the manuscript has been improved” with “new analyses [that] provide improved rigor”.

Despite these, the final eLife assessment inexplicably downplayed the significance of the findings and strength of evidence.

Broader Impact and Significance. The findings, not only the data, have theoretical and/or practical implications extending well beyond a single subfield relevant to:

1. behavioral neuroscientists studying sensorimotor integration

2. systems and theoretical neuroscientists

3. neural and biomechanical engineers working on brain-computer interfaces for speech or oral or limb prosthetics

4. soft robotics researchers

5. comparative motor control researchers

6. clinicians involved in the evaluation and rehabilitation of orolingual function (e.g., after stroke or glossectomy, dysphagia)

Given this broad relevance, we question why the significance was characterized as merely "useful" rather than "important."

Dismissive Tone Toward Descriptive Research. Some reviews displayed a dismissive or skeptical tone of the findings and their significance, even when methods were solid and support for the claims were strong. They critiqued the “descriptive nature” of our study, faulting the lack of mechanistic explanation. However, in poorly understood fields such as orofacial sensorimotor control, descriptive studies provide the empirical foundation for mechanistic studies. Rich descriptive data generate testable hypotheses that drive mechanistic discoveries forward, while mechanistic studies conducted without this groundwork often pursue precise answers to poorly formulated questions.

Specific Issues with Reviews:

1. Significant omission in study description:

The eLife Assessment’s second sentence states: “The data, which include both electrophysiology and nerve block manipulations, will be of value to neuroscientists and

neural engineers interested in tongue use.”

This description omits our simultaneously recorded high-resolution 3D kinematics data—a significant oversight given that combining high-density electrophysiological recording from multiple cortical regions with high-resolution 3D tongue kinematics during naturalistic behaviors in non-human primates represents one of our study's key strengths. Currently, only two research labs in the US possess this capability.

2. Overemphasis on the “smaller” and “inconsistent” findings

While we acknowledge some inconsistent findings between animals, the reviews overemphasized these inconsistencies in ways that cast unwarranted doubt on our more significant and consistent results.

a. Reviewer 1: “[...] the discrepancies in tuning changes across the two NHPs, coupled with the overall exploratory nature of the study, render the interpretation of these subtle differences somewhat speculative. “[...] in some recording sessions, they blocked sensory feedback using bilateral nerve block injections, which seemed to result in fewer directionally tuned units and changes in the overall distribution of the preferred direction of the units.”

The skeptical tone of the critique is in opposition to Reviewer 3’s statement that: “the evidence for these claims were solid”. In this statement, the reviewer characterized our findings as “somewhat speculative”, seemingly overlooking robust and consistent changes we documented:

• “Following nerve block, MIo and SIo showed significant decreases in the proportion of directionally modulated neurons across both tasks (Fig. 10A; Chi-square, MIo: p <0.001, SIo: p < 0.05).”

• “Nerve block significantly altered PD distributions during both tasks. During feeding, MIo neurons in both subjects exhibited a significant clockwise shift in mean PD toward the center (0°), resulting in more uniform distributions (Fig. 11A; circular k-test, p < 0.01).”

These results were obtained through careful subsampling of trials with similar kinematics for both feeding and drinking tasks, ensuring that the tuning changes in the nerve block experiments could not be attributed to differing kinematics.

b. Reviewer 2: “One weakness of the current study is that there is substantial variability in results between monkeys.”

This vague critique, without specifying which results showed “substantial variability”, reads as though most findings were inconsistent, unfairly casting doubt on our study’s validity.

3. Inaccurate statements in the Reviewers’ summaries

Several reviewer statements contain factual inaccuracies:

a. Reviewer 2: “A majority of neurons in MIo and a (somewhat smaller) percentage of SIo modulated their firing rates during tongue movements, with different modulation depending on the direction of movement (i.e., exhibited directional tuning).”

Reviewer 2's characterization of directional tuning misrepresents our findings. We reported substantial differences in the proportion of directionally tuned neurons between MIo and SIo during the feeding task but a smaller difference in the drinking task:

• “The proportion of directionally tuned neurons [...] differed significantly between MIo and SIo during the feeding task in both subjects (Chi-square, p < 0.001). In rostral and caudal MIo, 80% of neurons were modulated to 3D direction (bootstrap, p < 0.05, Fig. 3B, left), compared to 52% in areas 1/2 and 3a/3b.

• “During drinking, the proportion of directionally modulated neurons was more similar between regions (69% in MIo vs. 60% in SIo: Chi-square, p > 0.05, Fig. 3B right).”

b. Reviewer 2: “There were differences observed in the proportion and extent of directional tuning between the feeding and licking behaviors, with stronger tuning overall during licking.”

Reviewer 2's claim about task differences directly contradicts our findings. We consistently reported stronger tuning in feeding compared to drinking across multiple measures:

• “The proportion of directionally tuned neurons was higher in the feeding vs. drinking task (Chi-square, p < 0.05, feeding: 72%, drinking: 66%)”;

• “Cumulative explained variance for the first three factors was higher in feeding (MIo: 82%, SIo: 81%) than in drinking (MIo: 74%, SIo: 63%)”;

• “Decoding using LSTM showed consistently higher accuracies in feeding compared to drinking regardless of the length of intervals used ..., behavioral window .., and directional angles ...”

These results were also summarized in the Discussion.

c. Reviewer 1: In Figure 12, factor 2 and 3 are plotted against each other? and factor 1 is left out?

Reviewer 1’s observation about Figure 12 is incorrect. Factor 1 was included: Top subplots (feeding) show Factor 1 vs 3 (MIo) and Factor 1 vs 2 (SIo) while the bottom subplots (drinking) show Factor 2 vs 3 (MIo) and Factor 1 vs 2 (SIo). We plotted the two latent factors with highest explained variance for clarity, though all 20 factors were included in intertrajectory distance calculations.

4. Framing and interpretive over-scrutiny

Several critiques targeted framing rather than methodological rigor and emphasized that interpretations were speculative even when appropriately hedged:

a. Reviewer 2: “A revised version of the manuscript incorporates more population-level analyses, but with inconsistent use of quantifications/statistics and without sufficient contextualization of what the reader is to make of these results.”

Reviewer 2 mentioned "inconsistent use of quantifications/statistics" without specifying which analyses were problematic or updating their summary to include our additional population-level findings.

b. Reviewer 2: “The described changes in tuning after nerve block could also be explained by changes in kinematics between these conditions, which temper the interpretation of these interesting results”

Despite our addressing kinematic concerns through subsampled data analysis, Reviewer 2 remained unsatisfied, contrasting sharply with Reviewer 3's assessment that our arguments were "convincing" with "solid" evidence.

c. Reviewer 2: “I am not convinced of the claim that tongue directional encoding fundamentally changes between drinking and feeding given the dramatically different kinematics and the involvement of other body parts like the jaw”

Reviewer 2 expressed skepticism about fundamental encoding differences between tasks, despite our comprehensive controls including subsampled data with similar kinematics and multiple verification analyses (equal neuron numbers, stable neurons, various interval lengths, behavioral windows, and directional angles).

Without describing why these analyses were insufficient, this criticism goes beyond methods or statistics. It casts doubt and challenges whether the conclusions are even worth drawing despite careful experimental controls.

d. Reviewer 2: “The manuscript states that "An alternative explanation be more statistical/technical in nature: that during feeding, there will be more variability in exactly what somatosensation afferent signals are being received from trial to trial (because slight differences in kinematics can have large differences in exactly where the tongue is and the where/when/how of what parts of it are touching other parts of the oral cavity)? This variability could "smear out" the apparent tuning using these types of trial-averaged analyses. Given how important proprioception and somatosensation are for not biting the tongue or choking, the speculation that somatosensory cortical activity is suppressed during feedback is very counter-intuitive to this reviewer".

By not updating this section, Reviewer 2 failed to acknowledge our responsive revisions, including Fano factor analysis showing higher variability in SIo during feeding versus drinking, and our updated discussion addressing their concerns about trial-to-trial variability: “Varying tongue shape, tongue’s contact with varying bolus properties (size and texture) and other oral structures (palate, teeth) may weaken the directional signal contained in SIo activity. Thus, small differences in tongue kinematics might create large differences in sensory signals across trials. When looking at trial-averaged signals, this natural variability could make the neural response patterns appear less precise or specific than they are. These are consistent with our findings that for both tasks, spiking variability was higher in SIo.”

Authors’ Response to Recommendations for the authors:

We thank the editors and the reviewers for their helpful comments. We have provided a response to reviewers’ recommendations and made some revisions on the manuscript. 

Reviewer #1 (Recommendations for the authors): 

In the newly added population factor analysis, several methodological decisions remain unclear to me:

In Figure 7, why do the authors compare the mean distance between conditions in the latent spaces of MIo and SIo? Since these latent spaces are derived separately, they exist on different scales (with MIo appearing roughly four times larger than SIo), and this discrepancy is reflected in the reported mean distances (Figure 7, inset plots). Wouldn't this undermine a direct comparison?

Thank you for this helpful feedback. The reviewer is correct that the latent spaces are derived separately for MIo and SIo, thus they exist on different scales as we have noted in the caption of Figure 7: “Axes for SIo are 1/4 scale of MIo.” 

To allow for a direct comparison between MIo and SIo, we corrected the analysis by comparing their normalized mean inter-trajectory distances obtained by first calculating the geometric index (GI) of the inter-trajectory distances, d, between each pair of population trajectories per region as: GI= (d₁-d₂)/ (d₁+d₂). We then performed the statistics on the GIs and found a significant difference between mean inter-trajectory distances in MIo vs. SIo. We performed the same analysis comparing the distance travelled between MIo and SIo trajectories by getting the normalized difference in distances travelled and still found a significant difference in both tasks. We have updated the results and figure inset to reflect these changes.

In Figure 12, unlike Figure 7 which shows three latent dimensions, only two factors are plotted. While the methods section describes a procedure for selecting the optimal number of latent factors, Figure 7 - figure supplement 3 shows that variance explained continues to increase up to about five latent dimensions across all areas. Why, then, are fewer dimensions shown?

Thank you for the opportunity to clarify the figure. The m obtained from the 3-fold crossvalidation varied for the full sample and was 20 factors for the subsample. We clarify that all statistical analyses were done using 20 latent factors. Using the full sample of neurons, the first 3 factors explained 81% of variance in feeding data compared to 71% in drinking data. When extended to 5 factors, feeding maintained its advantage with 91% variance explained versus 82% for drinking. Because feeding showed higher variance explained than drinking across 3 or 5 factors, only three factors were shown in Figure 7 for better visualization. We added this clarification to the Methods and Results.

Figure 12 shows the differences in the neural trajectories between the control and nerve block conditions. The control vs. nerve block comparison complicated the visualization of the results. Thus, we plotted only the two latent factors with the highest separation between population trajectories. This was clarified in the Methods and caption of Figure 12.

In Figure 12, factor 2 and 3 are plotted against each other? and factor 1 is left out?

This observation is incorrect; Factor 1 was included: Top subplots (feeding) show Factor 1 vs 3 (MIo) and Factor 1 vs 2 (SIo) while the bottom subplots (drinking) show Factor 2 vs 3 (MIo) and Factor 1 vs 2 (SIo).  We have clarified this in the Methods and caption of Figure 12.

Finally, why are factor analysis results shown only for monkey R? 

Factor analysis results were performed on both animals, but the results were shown only for monkey R to decrease the number of figures in the manuscript. Figure 7- figure supplement 1 shows the data for both monkeys. Here are the equivalent Figure 7 plots for monkey Y. 

Author response image 1.

Reviewer #2 (Recommendations for the authors): 

Overall, the manuscript has been improved. 

New analyses provide improved rigor (as just one example, organizing the feeding data into three-category split to better match the three-direction drinking data decoding analysis and also matching the neuron counts).

The updated nerve block change method (using an equal number of trials with a similar leftright angle of movement in the last 100 ms of the tongue trajectory) somewhat reduces my concern that kinematic differences could account for the neural changes, but on the other hand the neural analyses use 250 ms (meaning that the neural differences could be related to behavioral differences earlier in the trial). Why not subselect to trials with similar trajectories throughout the whole movement(or at least show that as an additional analysis, albeit one with lower trial counts). 

As the reviewer pointed out, selecting similar trajectories throughout the whole movement would result in lower trial counts that lead to poor statistical power. We think that the 100 ms prior to maximum tongue protrusion is a more important movement segment to control for similar kinematics between the control and nerve block conditions since this represents the subject’s intended movement endpoint. 

A lot of the Results seemed like a list of measurements without sufficient hand-holding or guide-posting to explain what the take-away for the reader should be. Just one example to make concrete this broadly-applicable feedback: "Cumulative explained variance for the first three factors was higher in feeding (MIo: 82%, SIo: 81%) than in drinking (MIo: 74%, SIo: 63%) when all neurons were used for the factor analysis (Fig. 7)": why should we care about 3 factors specifically? Does this mean that in feeding, the neural dimensionality is lower (since 3 factors explain more of it)? Does that mean feeding is a "simpler" behavior (which is counter-intuitive and does not conform to the authors' comments about the higher complexity of feeding). And from later in that paragraph: what are we do make of the differences in neural trajectory distances (aside from quantifying using a different metric the same larger changes in firing rates that could just as well be quantified as statistics across single-neuron PETHs)?

Thank you for the feedback on the writing style. We have made some revisions to describe the takeaway for the reader. That fewer latent factors explain 80% of the variance in the feeding data means that the underlying network activity is relatively simple despite apparent complexity. When neural population trajectories are farther away from each other in state space, it means that the patterns of activity across tongue directions are more distinct and separable, thus, less likely to be confused with each other. This signifies that neural representations of 3D tongue directions are more robust. When there is better neural discrimination and more reliable information processing, it is easier for downstream brain regions to distinguish between different tongue directions.  

The addition of more population-level analyses is nice as it provides a more efficient summary of the neural measurements. However, it's a surface-level dive into these methods; ultimately the goal of ensemble "computation through dynamics" analyses is to discover simpler structure / organizational principles at the ensemble level (i.e., show things not evidence from single neurons), rather than just using them as a way to summarize data. For instance, here neural rotations are remarked upon in the Results, without referencing influential prior work describing such rotations and why neural circuits may use this computational motif to separate out conditions and shape muscle activity-generating readouts (Churchland et al. Nature 2012 and subsequent theoretical iterations including the Russo et al.). That said, the Russo et al tangling study was well-referenced and the present tangling results were eGectively contextualized with respect to that paper in terms of the interpretation. I wish more of the results were interpreted with comparable depth. 

Speaking of Russo et al: the authors note qualitative differences in tangling between brain areas, but do not actually quantify tangling in either. These observations would be stronger if quantified and accompanied with statistics.

Contrary to the reviewer’s critique, we did frame these results in the context of structure/organizational principles at the ensemble level. We had already cited prior work of Churchland et al., 2012; Michaels et al., 2016and Russo et al., 2018. In the Discussion, Differences across behaviors, we wrote: “In contrast, MIo trajectories in drinking exhibited a consistent rotational direction regardless of spout location (Fig. 7). This may reflect a predominant non-directional information such as condition-independent time-varying spiking activity during drinking (Kaufman et al., 2016; Kobak et al., 2016; Arce-McShane et al., 2023).” 

Minor suggestions: 

Some typos, e.g. 

• no opening parenthesis in "We quantified directional differences in population activity by calculating the Euclidean distance over m latent factors)"

• missing space in "independent neurons(Santhanam et al., 2009;..."); 

• missing closing parentheses in "followed by the Posterior Inferior (Figure 3 - figure supplement 1."

There is a one-page long paragraph in the Discussion. Please consider breaking up the text into more paragraphs each organized around one key idea to aid readability.

Thank you, we have corrected these typos.

Could it be that the Kaufman et al 2013 reference was intended to be Kaufman et al 2015 eNeuro (the condition-invariant signal paper)?

Thank you, we have corrected this reference.

At the end of the Clinical Implications subsection of the Discussion, the authors note the growing field of brain-computer interfaces with references for motor read-out or sensory write-in of hand motor/sensory cortices, respectively. Given that this study looks at orofacial cortices, an even more clinically relevant development is the more recent progress in speech BCIs (two     recent reviews: https://www.nature.com/articles/s41583-024-00819-9, https://www.annualreviews.org/content/journals/10.1146/annurev-bioeng-110122012818) many of which record from human ventral motor cortex and aspirations towards FES-like approaches for orofacial movements (e.g., https://link.springer.com/article/10.1186/s12984-023-01272-y).  

Thank you, we have included these references.

Reviewer #3 (Recommendations for the authors): 

Major Suggestions 

(1) For the factor analysis of feeding vs licking, it appears that the factors were calculated separately for the two behaviors. It could be informative to calculate the factors under both conditions and project the neural data for the two behaviors into that space. The overlap/separations of the subspace could be informative. 

We clarify that we performed a factor analysis that included both feeding and licking for MIo, as stated in the Results: “To control for factors such as different neurons and kinematics that might influence the results, we performed factor analysis on stable neurons across both tasks using all trials (Fig. 7- figure supplement 2A) and using trials with similar kinematics (Fig. 7- figure supplement 2B).” We have revised the manuscript to reflect this more clearly.

(2) For the LSTM, the Factor analyses and the decoding it is unclear if the firing rates are mean subtracted and being normalized (the methods section was a little unclear). Typically, papers in the field either z-score the data or do a softmax.

The firing rates were z-scored for the LSTM and KNN. For the factor analysis, the spike counts were not z-scored, but the results were normalized. We clarified this in the Methods section.

Minor: 

Page 1: Abstract- '... how OSMCx contributes to...' 

Since there are no direct causal manipulations of OSMCx in this manuscript, this study doesn't directly study the OSMCx's contribution to movement - I would recommend rewording this sentence.

Similarly, Page 2: 'OSMCx plays an important role in coordination...' the citations in this paragraph are correlative, and do not demonstrate a causal role.

There are similar usages of 'OSMCx coordinates...' in other places e.g. Page 8. 

Thank you, we revised these sentences.

Page 7: the LSTM here has 400 units, which is a very large network and contains >12000 parameters. Networks of this size are prone to memorization, it would be wise to test the rsquare of the validation set against a shuGled dataset to see if the network is actually working as intended. 

Thank you for bringing up this important point of verifying that the network is learning meaningful patterns versus memorizing. Considering the size of our training samples, the ratio of samples to parameters is appropriate and thus the risk of memorization is low. Indeed, validation tests and cross-validation performed indicated expected network behavior and the R squared values obtained here were similar to those reported in our previous paper (Laurence-Chasen et al., 2023).

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

In their paper, Hosack and Arce-McShane investigate how the 3D movement direction of the tongue is represented in the orofacial part of the sensory-motor cortex and how this representation changes with the loss of oral sensation. They examine the firing patterns of neurons in the orofacial parts of the primary motor cortex (MIo) and somatosensory cortex (SIo) in non-human primates (NHPs) during drinking and feeding tasks. While recording neural activity, they also tracked the kinematics of tongue movement using biplanar videoradiography of markers implanted in the tongue. Their findings indicate that most units in both MIo and SIo are directionally tuned during the drinking task. However, during the feeding task, directional turning was more frequent in MIo units and less prominent in SIo units. Additionally, in some recording sessions, they blocked sensory feedback using bilateral nerve block injections, which resulted in fewer directionally tuned units and changes in the overall distribution of the preferred direction of the units.

Strengths:

The most significant strength of this paper lies in its unique combination of experimental tools. The author utilized a video-radiography method to capture 3D kinematics of the tongue movement during two behavioral tasks while simultaneously recording activity from two brain areas. Moreover, they employed a nerve-blocking procedure to halt sensory feedback. This specific dataset and experimental setup hold great potential for future research on the understudied orofacial segment of the sensory-motor area.

Weaknesses:

Aside from the last part of the result section, the majority of the analyses in this paper are focused on single units. I understand the need to characterize the number of single units that directly code for external variables like movement direction, especially for less-studied areas like the orofacial part of the sensory-motor cortex. However, as a field, our decadelong experience in the arm region of sensory-motor cortices suggests that many of the idiosyncratic behaviors of single units can be better understood when the neural activity is studied at the level of the state space of the population. By doing so, for the arm region, we were able to explain why units have "mixed selectivity" for external variables, why the tuning of units changes in the planning and execution phase of the movement, why activity in the planning phase does not lead to undesired muscle activity, etc. See (Gallego et al. 2017; Vyas et al. 2020; Churchland and Shenoy 2024) for a review. Therefore, I believe investigating the dynamics of the population activity in orofacial regions can similarly help the reader go beyond the peculiarities of single units and in a broader view, inform us if the same principles found in the arm region can be generalized to other segments of sensorymotor cortex.

We thank and agree with the reviewer on the value of information gained from studying population activity. We also appreciate that population analyses have led to the understanding that individual neurons have “mixed selectivity”. We have shown previously that OSMCx neurons exhibit mixed selectivity in their population activity and clear separation between latent factors associated with gape and bite force levels (Arce-McShane FI, Sessle BJ, Ram Y, Ross CF, Hatsopoulos NG (2023) Multiple regions of primate orofacial sensorimotor cortex encode bite force and gape. Front Systems Neurosci. doi: 10.3389/fnsys.2023.1213279. PMID: 37808467 PMCID: 10556252), and chew-side and food types (Li Z & Arce-McShane FI (2023). Cortical representation of mastication in the primate orofacial sensorimotor cortex. Program No. NANO06.05. 2023 Neuroscience Meeting Planner. Washington, D.C.: Society for Neuroscience, 2023. Online.). 

The primary goal of this paper was to characterize single units in the orofacial region and to do a follow-up paper on population activity. In the revised manuscript, we have now incorporated the results of population-level analyses. The combined results of the single unit and population analyses provide a deeper understanding of the cortical representation of 3D direction of tongue movements during natural feeding and drinking behaviors. 

Further, for the nerve-blocking experiments, the authors demonstrate that the lack of sensory feedback severely alters how the movement is executed at the level of behavior and neural activity. However, I had a hard time interpreting these results since any change in neural activity after blocking the orofacial nerves could be due to either the lack of the sensory signal or, as the authors suggest, due to the NHPs executing a different movement to compensate for the lack of sensory information or the combination of both of these factors. Hence, it would be helpful to know if the authors have any hint in the data that can tease apart these factors. For example, analyzing a subset of nerve-blocked trials that have similar kinematics to the control.

Thank you for bringing this important point. We agree with the reviewer that any change in the neural activity may be attributed to lack of sensory signal or to compensatory changes or a combination of these factors. To tease apart these factors, we sampled an equal number of trials with similar kinematics for both control and nerve block feeding sessions. We added clarifying description of this approach in the Results section of the revised manuscript: “To confirm this e ect was not merely due to altered kinematics, we conducted parallel analyses using carefully subsampled trials with matched kinematic profiles from both control and nerve-blocked conditions.”

Furthermore, we ran additional analysis for the drinking datasets by subsampling a similar distribution of drinking movements from each condition. We compared the neural data from an equal number of trials with a similar left-right angle of movement in the last 100 ms of the tongue trajectory, nearest the spout. We compared the directional tuning across an equal number of trials with a similar left-right angle of movement in the last 100 ms of the tongue trajectory, nearest the spout. These analyses that control for similar kinematics showed that there was still a decrease in the proportion of directionally modulated neurons with nerve block compared to the control. This confirms that the results may be attributed to the lack of tactile information. These are now integrated in the revised paper under Methods section: Directional tuning of single neurons, as well as Results section: E ects of nerve block: Decreased directional tuning of MIo and SIo neurons and Figure 10 – figure supplement 1.

Reviewer #2 (Public review):

Summary:

This manuscript by Hosack and Arce-McShane examines the directional tuning of neurons in macaque primary motor (MIo) and somatosensory (SIo) cortex. The neural basis of tongue control is far less studied than, for example, forelimb movements, partly because the tongue's kinematics and kinetics are difficult to measure. A major technical advantage of this study is using biplanar video-radiography, processed with modern motion tracking analysis software, to track the movement of the tongue inside the oral cavity. Compared to prior work, the behaviors are more naturalistic behaviors (feeding and licking water from one of three spouts), although the animals were still head-fixed.

The study's main findings are that:

• A majority of neurons in MIo and a (somewhat smaller) percentage of SIo modulated their firing rates during tongue movements, with different modulations depending on the direction of movement (i.e., exhibited directional tuning). Examining the statistics of tuning across neurons, there was anisotropy (e.g., more neurons preferring anterior movement) and a lateral bias in which tongue direction neurons preferred that was consistent with the innervation patterns of tongue control muscles (although with some inconsistency between monkeys).

• Consistent with this encoding, tongue position could be decoded with moderate accuracy even from small ensembles of ~28 neurons.

• There were differences observed in the proportion and extent of directional tuning between the feeding and licking behaviors, with stronger tuning overall during licking. This potentially suggests behavioral context-dependent encoding.

• The authors then went one step further and used a bilateral nerve block to the sensory inputs (trigeminal nerve) from the tongue. This impaired the precision of tongue movements and resulted in an apparent reduction and change in neural tuning in Mio and SIo.

Strengths:

The data are difficult to obtain and appear to have been rigorously measured, and provide a valuable contribution to this under-explored subfield of sensorimotor neuroscience. The analyses adopt well-established methods, especially from the arm motor control literature, and represent a natural starting point for characterizing tongue 3D direction tuning.

Weaknesses:

There are alternative explanations for some of the interpretations, but those interpretations are described in a way that clearly distinguishes results from interpretations, and readers can make their own assessments. Some of these limitations are described in more detail below.

One weakness of the current study is that there is substantial variability in results between monkeys, and that only one session of data per monkey/condition is analyzed (8 sessions total). This raises the concern that the results could be idiosyncratic. The Methods mention that other datasets were collected, but not analyzed because the imaging pre-processing is very labor-intensive. While I recognize that time is precious, I do think in this case the manuscript would be substantially strengthened by showing that the results are similar on other sessions.

We acknowledge the reviewer’s concern about inter-subject variability. Animal feeding and drinking behaviors are quite stable across sessions, thus, we do not think that additional sessions will address the concern that the results could be idiosyncratic. Each of the eight datasets analyzed here have su icient neural and kinematic data to capture neural and behavioral patterns.  Nevertheless, we performed some of the analyses on a second feeding dataset from Monkey R. The results from analyses on a subset of this data were consistent across datasets; for example, (1) similar proportions of directionally tuned neurons, (2) similar distances between population trajectories (t-test p > 0.9), and (3) a consistently smaller distance between Anterior-Posterior pairs than others in MIo (t-test p < 0.05) but not SIo (p > 0.1). 

This study focuses on describing directional tuning using the preferred direction (PD) / cosine tuning model popularized by Georgopoulous and colleagues for understanding neural control of arm reaching in the 1980s. This is a reasonable starting point and a decent first-order description of neural tuning. However, the arm motor control field has moved far past that viewpoint, and in some ways, an over-fixation on static representational encoding models and PDs held that field back for many years. The manuscript benefits from drawing the readers' attention (perhaps in their Discussion) that PDs are a very simple starting point for characterizing how cortical activity relates to kinematics, but that there is likely much richer population-level dynamical structure and that a more mechanistic, control-focused analytical framework may be fruitful. A good review of this evolution in the arm field can be found in Vyas S, Golub MD, Sussillo D, Shenoy K. 2020. Computation Through Neural Population Dynamics. Annual Review of Neuroscience. 43(1):249-75

Thank you for highlighting this important point. Research on orofacial movements hasn't progressed at the same pace as limb movement studies. Our manuscript focused specifically on characterizing the 3D directional tuning properties of individual neurons in the orofacial area—an analysis that has not been conducted previously for orofacial sensorimotor control. While we initially prioritized this individual neuron analysis, we recognize the value of broader population-level insights.

Based on your helpful feedback, we have incorporated additional population analyses to provide a more comprehensive picture of orofacial sensorimotor control and expanded our discussion section. We appreciate your expertise in pushing our work to be more thorough and aligned with current neuroscience approaches.

Can the authors explain (or at least speculate) why there was such a large difference in behavioral e ect due to nerve block between the two monkeys (Figure 7)?

We acknowledge this as a variable inherent to this type of experimentation. Previous studies have found large kinematic variation in the effect of oral nerve block as well as in the following compensatory strategies between subjects. Each animal’s biology and response to perturbation vary naturally. Indeed, our subjects exhibited different feeding behavior even in the absence of nerve block perturbation (see Figure 2 in Laurence-Chasen et al., 2022). This is why each individual serves as its own control.

Do the analyses showing a decrease in tuning after nerve block take into account the changes (and sometimes reduction in variability) of the kinematics between these conditions? In other words, if you subsampled trials to have similar distributions of kinematics between Control and Block conditions, does the effect hold true? The extreme scenario to illustrate my concern is that if Block conditions resulted in all identical movements (which of course they don't), the tuning analysis would find no tuned neurons. The lack of change in decoding accuracy is another yellow flag that there may be a methodological explanation for the decreased tuning result.

Thank you for bringing up this point. We accounted for the changes in the variability of the kinematics between the control and nerve block conditions in the feeding dataset where we sampled an equal number of trials with similar kinematics for both control and nerve block. However, we did not control for similar kinematics in the drinking task. In the revised manuscript, we have clarified this and performed similar analysis for the drinking task. We sampled a similar distribution of drinking movements from each condition. We compared the neural data from an equal number of trials with a similar left-right angle of movement in the last 100 ms of the tongue trajectory, nearest the spout. There was a decrease in the percentage of neurons that were directionally modulated (between 30 and 80%) with nerve block compared to the control. These results have been included in the revised paper under Methods section: Directional tuning of single neurons, as well as Results section: E ects of nerve block: Decreased directionality of MIo and SIo neurons.

While the results from decoding using KNN did not show significant differences between decoding accuracies in control vs. nerve block conditions, the results from the additional factor analysis and decoding using LSTM were consistent with the decrease in directional tuning at the level of individual neurons.  

The manuscript states that "Our results suggest that the somatosensory cortex may be less involved than the motor areas during feeding, possibly because it is a more ingrained and stereotyped behavior as opposed to tongue protrusion or drinking tasks". Could an alternative explanation be more statistical/technical in nature: that during feeding, there will be more variability in exactly what somato sensation afferent signals are being received from trial to trial (because slight differences in kinematics can have large differences in exactly where the tongue is and the where/when/how of what parts of it are touching other parts of the oral cavity)? This variability could "smear out" the apparent tuning using these types of trial-averaged analyses. Given how important proprioception and somatosensation are for not biting the tongue or choking, the speculation that somatosensory cortical activity is suppressed during feedback is very counter-intuitive to this reviewer.

Thank you for bringing up this point. We have now incorporated this in our revised Discussion (see Comparison between MIo and SIo). We agree with the reviewer that trialby-trial variability in the a erent signals may account for the lower directional signal in SIo during feeding than in drinking. Indeed, SIo’s mean-matched Fano factor in feeding was significantly higher than those in drinking (Author response image 1). Moreover, the results of the additional population and decoding analyses also support this.  

Author response image 1.

Comparison of mean-matched Fano Factor between Sio neurons during feeding and drinking control tasks across both subjects (Wilcoxon rank sum test, p < 0.001).

Reviewer #3 (Public review):

Summary:

In this study, the authors aim to uncover how 3D tongue direction is represented in the Motor (M1o) and Somatosensory (S1o) cortex. In non-human primates implanted with chronic electrode arrays, they use X-ray-based imaging to track the kinematics of the tongue and jaw as the animal is either chewing food or licking from a spout. They then correlate the tongue kinematics with the recorded neural activity. Using linear regressions, they characterize the tuning properties and distributions of the recorded population during feeding and licking. Then, they recharacterize the tuning properties after bilateral lidocaine injections in the two sensory branches of the trigeminal nerve. They report that their nerve block causes a reorganization of the tuning properties. Overall, this paper concludes that M1o and S1o both contain representations of the tongue direction, but their numbers, their tuning properties, and susceptibility to perturbed sensory input are different.

Strengths:

The major strengths of this paper are in the state-of-the-art experimental methods employed to collect the electrophysiological and kinematic data.

Weaknesses:

However, this paper has a number of weaknesses in the analysis of this data.

It is unclear how reliable the neural responses are to the stimuli. The trial-by-trial variability of the neural firing rates is not reported. Thus, it is unclear if the methods used for establishing that a neuron is modulated and tuned to a direction are susceptible to spurious correlations. The authors do not use shuffling or bootstrapping tests to determine the robustness of their fits or determining the 'preferred direction' of the neurons. This weakness colors the rest of the paper.

Thank you for raising these points. We have performed the following additional analyses: (1) We have added analyses to ensure that the results could not be explained by neural variability. To show the trial-by-trial variability of the neural firing rates, we have calculated the Fano factor (mean overall = 1.34747; control = 1.46471; nerve block = 1.23023). The distribution was similar across directions, suggesting that responses of MIo and SIo neurons to varying 3D directions were reliable. (2) We have used a bootstrap procedure to ensure that directional tuning cannot be explained by mere chance. (3) To test the robustness of our PDs we also performed a bootstrap test, which yielded the same results for >90% of neurons, and a multiple linear regression test for fit to a cosine-tuning function. In the revised manuscript, the Methods and Results sections have been updated to include these analyses.  

Author response image 2.

Comparison of Fano Factor across directions for MIo and SIo Feeding Control (Kruskal-Wallis, p > 0.7).

The authors compare the tuning properties during feeding to those during licking but only focus on the tongue-tip. However, the two behaviors are different also in their engagement of the jaw muscles. Thus many of the differences observed between the two 'tasks' might have very little to do with an alternation in the properties of the neural code - and more to do with the differences in the movements involved. 

Using the tongue tip for the kinematic analysis of tongue directional movements was a deliberate choice as the anterior region of the tongue is highly mobile and sensitive due to a higher density of mechanoreceptors. The tongue tip is the first region that touches the spout in the drinking task and moves the food into the oral cavity for chewing and subsequent swallowing. 

We agree with the reviewer that the jaw muscles are engaged differently in feeding vs. drinking (see Fig. 2). For example, a wider variety of jaw movements along the three axes are observed in feeding compared to the smaller amplitude and mostly vertical jaw movements in drinking. Also, the tongue movements are very different between the two behaviors. In feeding, the tongue moves in varied directions to position the food between left-right tooth rows during chewing, whereas in the drinking task, the tongue moves to discrete locations to receive the juice reward. Moreover, the tongue-jaw coordination differs between tasks; maximum tongue protrusion coincides with maximum gape in drinking but with minimum gape in the feeding behavior. Thus, the different tongue and jaw movements required in each behavior may account for some of the differences observed in the directional tuning properties of individual neurons and population activity. These points have been included in the revised Discussion.

Author response image 3.

Tongue tip position (mm) and jaw pitch(degree) during feeding (left) and drinking (right) behaviors. Most protruded tongue position coincides with minimum gape (jaw pitch at 0°) during  feeding but with maximum gape during drinking.

Many of the neurons are likely correlated with both Jaw movements and tongue movements - this complicates the interpretations and raises the possibility that the differences in tuning properties across tasks are trivial.

We thank the reviewer for raising this important point. In fact, we verified in a previous study whether the correlation between the tongue and jaw kinematics might explain differences in the encoding of tongue kinematics and shape in MIo (see Supplementary Fig. 4 in Laurence-Chasen et al., 2023): “Through iterative sampling of sub-regions of the test trials, we found that correlation of tongue kinematic variables with mandibular motion does not account for decoding accuracy. Even at times where tongue motion was completely un-correlated with the jaw, decoding accuracy could be quite high.” 

The results obtained from population analyses showing distinct properties of population trajectories in feeding vs. drinking behaviors provide strong support to the interpretation that directional information varies between these behaviors.

The population analyses for decoding are rudimentary and provide very coarse estimates (left, center, or right), it is also unclear what the major takeaways from the population decoding analyses are. The reduced classification accuracy could very well be a consequence of linear models being unable to account for the complexity of feeding movements, while the licking movements are 'simpler' and thus are better accounted for.

We thank the reviewer for raising this point. The population decoding analyses provide additional insight on the directional information in population activity,  as well as a point of comparison with the results of numerous decoding studies on the arm region of the sensorimotor cortex. In the revised version, we have included the results from decoding tongue direction using a long short-term memory (LSTM) network for sequence-tosequence decoding. These results differed from the KNN results, indicating that a linear model such as KNN was better for drinking and that a non-linear and continuous decoder was better suited for feeding.  These results have been included in the revised manuscript.

The nature of the nerve block and what sensory pathways are being affected is unclear - the trigeminal nerve contains many different sensory afferents - is there a characterization of how e ectively the nerve impulses are being blocked? Have the authors confirmed or characterized the strength of their inactivation or block, I was unable to find any electrophysiological evidence characterizing the perturbation.

The strength of the nerve block is characterized by a decrease in the baseline firing rate of SIo neurons, as shown in Supplementary Figure 6 of “Loss of oral sensation impairs feeding performance and consistency of tongue–jaw coordination” (Laurence-Chasen et al., 2022)..

Overall, while this paper provides a descriptive account of the observed neural correlations and their alteration by perturbation, a synthesis of the observed changes and some insight into neural processing of tongue kinematics would strengthen this paper.

We thank the reviewer for this suggestion. We have revised the Discussion to provide a synthesis of the results and insights into the neural processing of tongue kinematics.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) The procedure for anesthesia explained in the method section was not clear to me. The following information was missing: what drug/dose was used? How long the animal was under anesthesia? How long after the recovery the experiments were done?

The animals were fully sedated with ketamine (100 mg/ml, 10 mg/kg) for less than 30 minutes, and all of the data was collected within 90 minutes after the nerve block was administered.

(2) In Figure 10, panels A and B are very close together, it was not at first clear whether the text "Monkey R, Monkey Y" belongs to panel A or B.

We have separated the two panels further in the revised figure.

(3) I found Figure 11 very busy and hard to interpret. Separating monkeys, fitting the line for each condition, or using a bar plot can help with the readability of the figure.

Thank you for the suggestion. We agree with you and have reworked this figure. To simplify it we have shown the mean accuracy across iterations.

(4) I found the laterality discussions like "This signifies that there are more neurons in the left hemisphere contributes toward one direction of tongue movement, suggesting that there is some laterality in the PDs of OSMCx neurons that varies between individuals" bit of an over-interpretation of data, given the low n value and the dissimilarity in how strongly the nerve blocking altered monkies behavior.

Thank you for sharing this viewpoint. We do think that laterality is a good point of comparison with studies on M1 neurons in the arm/hand region. In our study, we found that the peak of the PD distribution coincides with leftward tongue movements in feeding. The distribution of PDs provides insight into how tongue muscles are coordinated during movement. Intrinsic and extrinsic tongue muscles are involved in shaping the tongue (e.g., elongation, broadening) and positioning the tongue (e.g., protrusion/retraction, elevation/depression), respectively. These muscles receive bilateral motor innervation except for genioglossus. Straight tongue protrusion requires the balanced action of the right and left genioglossi while the lateral protrusion involves primarily the contralateral genioglossus. Given this unilateral innervation pattern, we hypothesized that left MIo/SIo neurons would preferentially respond to leftward tongue movements, corresponding to right genioglossus activation. 

Reviewer #2 (Recommendations for the authors):

Are the observation of tuning peaks being most frequently observed toward the anterior and superior directions consistent with the statistics of the movements the tongue typically makes? This could be analogous to anisotropies previously reported in the arm literature, e.g., Lillicrap TP, Scott SH. 2013. Preference Distributions of Primary Motor Cortex Neurons Reflect Control Solutions Optimized for Limb Biomechanics. Neuron. 77(1):168-79

Thank you for bringing our attention to analogous findings by Lillicrap & Scott, 2013. Indeed, we do observe the highest number of movements in the Anterior Superior directions, followed by the Posterior Inferior. This does align with the distribution of tuning peaks that we observed. Author response image 4 shows the proportions of observed movements in each group of directions across all feeding datasets. We have incorporated this data in the Results section: Neuronal modulation patterns differ between MIo and SIo, as well as added this point in the Discussion.

Author response image 4.

Proportion of feeding trials in each group of directions. Error bars represent ±1 standard deviation across datasets (n = 4).

"The Euclidean distance was used to identify nearest neighbors, and the number of nearest neighbors used was K = 7. This K value was determined after testing different Ks which yielded comparable results." In general, it's a decoding best practice to tune hyperparameters (like K) on fully held-out data from the data used for evaluation. Otherwise, this tends to slightly inflate performance because one picks the hyperparameter that happened to give the best result. It sounds like that held-out validation set wasn't used here. I don't think that's going to change the results much at all (especially given the "comparable results" comment), but providing this suggestion for the future. If the authors replicate results on other datasets, I suggest they keep K = 7 to lock in the method.

K = 7 was chosen based on the size of our smallest training dataset (n = 55). The purpose of testing different K values was not to select which value gave the best result, but to demonstrate that similar K values did not affect the results significantly. We tested the different K values on a subset of the feeding data, but that data was not fully held-out from the training set. We will keep your suggestion in mind for future analysis.

The smoothing applied to Figure 2 PSTHs appears perhaps excessive (i.e., it may be obscuring interesting finer-grained details of these fast movements). Can the authors reduce the 50 ms Gaussian smoothing (I assume this is the s.d.?) ~25 ms is often used in studying arm kinematics. It also looks like the movement-related modulation may not be finished in these 200 ms / 500 ms windows. I suggest extending the shown time window. It would also be helpful to show some trial-averaged behavior (e.g. speed or % displacement from start) under or behind the PSTHs, to give a sense of what phase of the movement the neural activity corresponds to.

Thank you for the suggestion. We have taken your suggestions into consideration and modified Figure 2 accordingly. We decreased the Gaussian kernel to 25 ms and extended the time window shown. The trial-averaged anterior/posterior displacement was also added to the drinking PSTHs.

Reviewer #3 (Recommendations for the authors):

The major consideration here is that the data reported for feeding appears to be very similar to that reported in a previous study:

"Robust cortical encoding of 3D tongue shape during feeding in macaques"

Are the neurons reported here the same as the ones used in this previous paper? It is deeply concerning that this is not reported anywhere in the methods section.

These are the same neurons as in our previous paper, though here we include several additional datasets of the nerve block and drinking sessions. We have now included this in the methods section.

Second, I strongly recommend that the authors consider a thorough rewrite of this manuscript and improve the presentation of the figures. As written, it was not easy to follow the paper, the logic of the experiments, or the specific data being presented in the figures.

Thank you for this suggestion. We have done an extensive rewrite of the manuscript and revision of the figures.

A few recommendations:

(1) Please structure your results sections and use descriptive topic sentences to focus the reader. In the current version, it is unclear what the major point being conveyed for each analysis is.

Thank you for this suggestion. We have added topic sentences to the begin each section of the results.

(2) Please show raster plots for at least a few example neurons so that the readers have a sense of what the neural responses look like across trials. Is all of Figure 2 one example neuron or are they different neurons? Error bars for PETH would be useful to show the reliability and robustness of the tuning.

Figure 2 shows different neurons, one from MIo and one from SIo for each task. There is shading showing ±1 standard error around the line for each direction, however this was a bit difficult to see. In addition to the other changes we have made to these figures, we made the lines smaller and darkened the error bar shading to accentuate this. We also added raster plots corresponding to the same neurons represented in Figure 2 as a supplement.

(3) Since there are only two data points, I am not sure I understand why the authors have bar graphs and error bars for graphs such as Figure 3B, Figure 5B, etc. How can one have an error bar and means with just 2 data points?

Those bars represent the standard error of the proportion. We have changed the y-axis label on these figures to make this clearer.

(4) Results in Figure 6 could be due to differential placement of the electrodes across the animals. How is this being accounted for?

Yes, this is a possibility which we have mentioned in the discussion. Even with careful placement there is no guarantee to capture a set of neurons with the exact same function in two subjects, as every individual is different. Rather we focus on analyses of data within the same animal. The purpose of Figure 6 is to show the difference between MIo and SIo, and between the two tasks, within the same subject. The more salient result from calculating the preferred direction is that there is a change in the distribution between control and nerve block within the same exact population. Discussions relating to the comparison between individuals are speculative and cannot be confirmed without the inclusion of many more subjects.

(5) For Figure 7, I would recommend showing the results of the Sham injection in the same figure instead of a supplement.

Thank you for the suggestion, we have added these results to the figure.

(6) I think the e ects of the sensory block on the tongue kinematics are underexplored in Figure 7 and Figure 8. The authors could explore the deficits in tongue shape, and the temporal components of the trajectory.

Some of these effects on feeding have been explored in a previous paper, LaurenceChasen et al., 2022. We performed some additional analyses on changes to kinematics during drinking, including the number of licks per 10 second trial and the length of individual licks. The results of these are included below. We also calculated the difference in the speed of tongue movement during drinking, which generally decreased and exhibited an increase in variance with nerve block (f-test, p < 0.001). However, we have not included these figures in the main paper as they do not inform us about directionality.

Author response image 5.

Left halves of hemi-violins (black) are control and right halves (red) are nerve block for an individual. Horizontal black lines represent the mean and horizontal red lines the median. Results of two-tailed t-test and f-test are indicated by asterisks and crosses, respectively: *,† p < 0.05; **,†† p < 0.01; ***,††† p < 0.001.

(9) In Figures 9 and 10. Are the same neurons being recorded before and after the nerve block? It is unclear if the overall "population" properties are different, or if the properties of individual neurons are changing due to the nerve block.

Yes, the same neurons are being recorded before and after nerve block. Specifically, Figure 9B shows that the properties of many individual neurons do change due to the nerve block. Differences in the overall population response may be attributed to some of the units having reduced/no activity during the nerve block session.

Additionally, I recommend that the authors improve their introduction and provide more context to their discussion. Please elaborate on what you think are the main conceptual advances in your study, and place them in the context of the existing literature. By my count, there are 26 citations in this paper, 4 of which are self-citations - clearly, this can be improved upon.

Thank you for this suggestion. We have done an extensive rewrite of the Introduction and Discussion. We discussed the main conceptual advances in our study and place them in the context of the existing literature.

Reviewer #2 (Public review):

Summary:

This manuscript by Hosack and Arce-McShane examines the directional tuning of neurons in macaque primary motor (MIo) and somatosensory (SIo) cortex. The neural basis of tongue control is far less studied than, for example, forelimb movements, partly because the tongue's kinematics and kinetics are difficult to measure. A major technical advantage of this study is using biplanar video-radiography, processed with modern motion tracking analysis software, to track the movement of the tongue inside the oral cavity. Compared to prior work, the behaviors are more naturalistic behaviors (feeding and licking water from one of three spouts), although the animals were still head-fixed.

The study's main findings are that:

• A majority of neurons in MIo and a (somewhat smaller) percentage of SIo modulated their firing rates during tongue movements, with different modulation depending on the direction of movement (i.e., exhibited directional tuning). Examining the statistics of tuning across neurons, there was anisotropy (e.g., more neurons preferring anterior movement) and a lateral bias in which tongue direction neurons preferred that was consistent with the innervation patterns of tongue control muscles (although with some inconsistency between monkeys).<br /> • Consistent with this encoding, tongue position could be decoded with moderate accuracy even from small ensembles of ~28 neurons.<br /> • There were differences observed in the proportion and extent of directional tuning between the feeding and licking behaviors, with stronger tuning overall during feeding. This potentially suggests behavioral context-dependent encoding.<br /> • The authors then went one step further and used a bilateral nerve block to the sensory inputs (trigeminal nerve) from the tongue. This impaired the precision of tongue movements and resulted in an apparent reduction and change in neural tuning in Mio and SIo.

Strengths:

The data are difficult to obtain and appear to have been rigorously measured, and provide a valuable contribution to this under-explored subfield of sensorimotor neuroscience. The analyses adopt well-established methods especially from the arm motor control literature, and represent a natural starting point for characterizing tongue 3D direction tuning.

Weaknesses:

There are alternative explanations from some of the interpretations, but those interpretations are described in a way that clearly distinguishes results from interpretations, and readers can make their own assessments. Some of these limitations are described in more detail below.

One weakness of the current study is that there is substantial variability in some of the results between monkeys, including the tuning characteristics of primary somatosensory cortex neurons during drinking, and the effect of nerve block on tongue movements and the associated changes in single neuron tuning.

This study focuses on describing directional tuning using the preferred direction (PD) / cosine tuning model popularized by Georgopoulous and colleagues for understanding neural control of arm reaching in the 1980s. This is a reasonable starting point and a decent first order description of neural tuning. However, the arm motor control field has moved far past that viewpoint, and in some ways an over-fixation on static representational encoding models and PDs held that field back for many years. The manuscript benefit from drawing the readers' attention (perhaps in their Discussion) that PDs are a very simple starting point for characterizing how cortical activity relates to kinematics, but that there is likely much richer population-level dynamical structure and that a more mechanistic, control-focused analytical framework may be fruitful. A good review of this evolution in the arm field can be found in Vyas S, Golub MD, Sussillo D, Shenoy K. 2020. Computation Through Neural Population Dynamics. Annual Review of Neuroscience. 43(1):249-75. A revised version of the manuscript incorporates more population-level analyses, but with inconsistent use of quantifications/statistics and without sufficient contextualization of what the reader is to make of these results.

The described changes in tuning after nerve block could also be explained by changes in kinematics between these conditions, which temper the interpretation of these interesting results.

I am not convinced of the claim that tongue directional encoding fundamentally changes between drinking and feeding given the dramatically different kinematics and the involvement of other body parts like the jaw (e.g., the reference to Laurence-Chasen et al. 2023 just shows that there is tongue information independent of jaw kinematics, not that jaw movements don't affect these neurons' activities). I also find the nerve block results inconsistent (more tuning in one monkey, less in the other?) and difficult to really learn something fundamental from, besides that neural activity and behavior both change - in various ways - after nerve block (not at all surprising but still good to see measurements of).

The manuscript states that "Our results suggest that the somatosensory cortex may be less involved than the motor areas during feeding, possibly because it is a more ingrained and stereotyped behavior as opposed to tongue protrusion or drinking tasks". An alternative explanation be more statistical/technical in nature: that during feeding, there will be more variability in exactly what somatosensation afferent signals are being received from trial to trial (because slight differences in kinematics can have large differences in exactly where the tongue is and the where/when/how of what parts of it are touching other parts of the oral cavity)? This variability could "smear out" the apparent tuning using these types of trial-averaged analyses. Given how important proprioception and somatosensation are for not biting the tongue or choking, the speculation that somatosensory cortical activity is suppressed during feedback is very counter-intuitive to this reviewer. In the revised manuscript the authors note these potential confounds and other limitations in the Discussion.

Author response:

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

eLife Assessment

This valuable study investigates how the neural representation of individual finger movements changes during the early period of sequence learning. By combining a new method for extracting features from human magnetoencephalography data and decoding analyses, the authors provide incomplete evidence of an early, swift change in the brain regions correlated with sequence learning, including a set of previously unreported frontal cortical regions. The addition of more control analyses to rule out that head movement artefacts influence the findings, and to further explain the proposal of offline contextualization during short rest periods as the basis for improvement performance would strengthen the manuscript.

We appreciate the Editorial assessment on our paper’s strengths and novelty. We have implemented additional control analyses to show that neither task-related eye movements nor increasing overlap of finger movements during learning account for our findings, which are that contextualized neural representations in a network of bilateral frontoparietal brain regions actively contribute to skill learning. Importantly, we carried out additional analyses showing that contextualization develops predominantly during rest intervals.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study addresses the issue of rapid skill learning and whether individual sequence elements (here: finger presses) are differentially represented in human MEG data. The authors use a decoding approach to classify individual finger elements and accomplish an accuracy of around 94%. A relevant finding is that the neural representations of individual finger elements dynamically change over the course of learning. This would be highly relevant for any attempts to develop better brain machine interfaces - one now can decode individual elements within a sequence with high precision, but these representations are not static but develop over the course of learning.

Strengths:

The work follows a large body of work from the same group on the behavioural and neural foundations of sequence learning. The behavioural task is well established and neatly designed to allow for tracking learning and how individual sequence elements contribute. The inclusion of short offline rest periods between learning epochs has been influential because it has revealed that a lot, if not most of the gains in behaviour (ie speed of finger movements) occur in these socalled micro-offline rest periods. The authors use a range of new decoding techniques, and exhaustively interrogate their data in different ways, using different decoding approaches. Regardless of the approach, impressively high decoding accuracies are observed, but when using a hybrid approach that combines the MEG data in different ways, the authors observe decoding accuracies of individual sequence elements from the MEG data of up to 94%.

We have previously showed that neural replay of MEG activity representing the practiced skill was prominent during rest intervals of early learning, and that the replay density correlated with micro-offline gains (Buch et al., 2021). These findings are consistent with recent reports (from two different research groups) that hippocampal ripple density increases during these inter-practice rest periods, and predict offline learning gains (Chen et al., 2024; Sjøgård et al., 2024). However, decoder performance in our earlier work (Buch et al., 2021) left room for improvement. Here, we reported a strategy to improve decoding accuracy that could benefit future studies of neural replay or BCI using MEG.

Weaknesses:

There are a few concerns which the authors may well be able to resolve. These are not weaknesses as such, but factors that would be helpful to address as these concern potential contributions to the results that one would like to rule out. Regarding the decoding results shown in Figure 2 etc, a concern is that within individual frequency bands, the highest accuracy seems to be within frequencies that match the rate of keypresses. This is a general concern when relating movement to brain activity, so is not specific to decoding as done here. As far as reported, there was no specific restraint to the arm or shoulder, and even then it is conceivable that small head movements would correlate highly with the vigor of individual finger movements. This concern is supported by the highest contribution in decoding accuracy being in middle frontal regions - midline structures that would be specifically sensitive to movement artefacts and don't seem to come to mind as key structures for very simple sequential keypress tasks such as this - and the overall pattern is remarkably symmetrical (despite being a unimanual finger task) and spatially broad. This issue may well be matching the time course of learning, as the vigor and speed of finger presses will also influence the degree to which the arm/shoulder and head move. This is not to say that useful information is contained within either of the frequencies or broadband data. But it raises the question of whether a lot is dominated by movement "artefacts" and one may get a more specific answer if removing any such contributions.

Reviewer #1 expresses concern that the combination of the low-frequency narrow-band decoder results, and the bilateral middle frontal regions displaying the highest average intra-parcel decoding performance across subjects is suggestive that the decoding results could be driven by head movement or other artefacts.

Head movement artefacts are highly unlikely to contribute meaningfully to our results for the following reasons. First, in addition to ICA denoising, all “recordings were visually inspected and marked to denoise segments containing other large amplitude artifacts due to movements” (see Methods). Second, the response pad was positioned in a manner that minimized wrist, arm or more proximal body movements during the task. Third, while online monitoring of head position was not performed for this study, it was assessed at the beginning and at the end of each recording. The head was restrained with an inflatable air bladder, and head movement between the beginning and end of each scan did not exceed 5mm for all participants included in the study.

The Reviewer states a concern that “it is conceivable that small head movements would correlate highly with the vigor of individual finger movements”. We agree that despite the steps taken above, it is possible that minor head movements could still contribute to some remaining variance in the MEG data in our study. However, such correlations between small head movements and finger movements could only meaningfully contribute to decoding performance if: (A) they were consistent and pervasive throughout the recording (which might not be the case if the head movements were related to movement vigor and vigor changed over time); and (B) they systematically varied between different finger movements, and also between the same finger movement performed at different sequence locations (see 5-class decoding performance in Figure 4B). The possibility of any head movement artefacts meeting all these conditions is unlikely. Alternatively, for this task design a much more likely confound could be the contribution of eye movement artefacts to the decoder performance (an issue raised by Reviewer #3 in the comments below).

Remember from Figure 1A in the manuscript that an asterisk marks the current position in the sequence and is updated at each keypress. Since participants make very few performance errors, the position of the asterisk on the display is highly correlated with the keypress being made in the sequence. Thus, it is possible that if participants are attending to the visual feedback provided on the display, they may generate eye movements that are systematically related to the task. Since we did record eye movements simultaneously with the MEG recordings (EyeLink 1000 Plus; Fs = 600 Hz), we were able to perform a control analysis to address this question. For each keypress event during trials in which no errors occurred (which is the same time-point that the asterisk position is updated), we extracted three features related to eye movements: 1) the gaze position at the time of asterisk position update (triggered by a KeyDown event), 2) the gaze position 150ms later, and 3) the peak velocity of the eye movement between the two positions. We then constructed a classifier from these features with the aim of predicting the location of the asterisk (ordinal positions 1-5) on the display. As shown in the confusion matrix below (Author response image 1), the classifier failed to perform above chance levels (overall cross-validated accuracy = 0.21817):

Author response image 1.

Confusion matrix showing that three eye movement features fail to predict asterisk position on the task display above chance levels (Fold 1 test accuracy = 0.21718; Fold 2 test accuracy = 0.22023; Fold 3 test accuracy = 0.21859; Fold 4 test accuracy = 0.22113; Fold 5 test accuracy = 0.21373; Overall cross-validated accuracy = 0.2181). Since the ordinal position of the asterisk on the display is highly correlated with the ordinal position of individual keypresses in the sequence, this analysis provides strong evidence that keypress decoding performance from MEG features is not explained by systematic relationships between finger movement behavior and eye movements (i.e. – behavioral artefacts) (end of figure legend).

Remember that the task display does not provide explicit feedback related to performance, only information about the present position in the sequence. Thus, it is possible that participants did not actively attend to the feedback. In fact, inspection of the eye position data revealed that on majority of trials, participants displayed random-walk-like gaze patterns around a central fixation point located near the center of the screen. Thus, participants did not attend to the asterisk position on the display, but instead intrinsically generated the action sequence. A similar realworld example would be manually inputting a long password into a secure online application. In this case, one intrinsically generates the sequence from memory and receives similar feedback about the password sequence position (also provided as asterisks) as provided in the study task – feedback which is typically ignored by the user.

The minimal participant engagement with the visual task display observed in this study highlights another important point – that the behavior in explicit sequence learning motor tasks is highly generative in nature rather than reactive to stimulus cues as in the serial reaction time task (SRTT). This is a crucial difference that must be carefully considered when designing investigations and comparing findings across studies.

We observed that initial keypress decoding accuracy was predominantly driven by contralateral primary sensorimotor cortex in the initial practice trials before transitioning to bilateral frontoparietal regions by trials 11 or 12 as performance gains plateaued. The contribution of contralateral primary sensorimotor areas to early skill learning has been extensively reported in humans and non-human animals.(Buch et al., 2021; Classen et al., 1998; Karni et al., 1995; Kleim et al., 1998) Similarly, the increased involvement of bilateral frontal and parietal regions to decoding during early skill learning in the non-dominant hand is well known. Enhanced bilateral activation in both frontal and parietal cortex during skill learning has been extensively reported (Doyon et al., 2002; Grafton et al., 1992; Hardwick et al., 2013; Kennerley et al., 2004; Shadmehr & Holcomb, 1997; Toni, Ramnani, et al., 2001), and appears to be even more prominent during early fine motor skill learning in the non-dominant hand (Lee et al., 2019; Sawamura et al., 2019). The frontal regions identified in these studies are known to play crucial roles in executive control (Battaglia-Mayer & Caminiti, 2019), motor planning (Toni, Thoenissen, et al., 2001), and working memory (Andersen & Buneo, 2002; Buneo & Andersen, 2006; Shadmehr & Holcomb, 1997; Toni, Ramnani, et al., 2001; Wolpert et al., 1998) processes, while the same parietal regions are known to integrate multimodal sensory feedback and support visuomotor transformations (Andersen & Buneo, 2002; Buneo & Andersen, 2006; Shadmehr & Holcomb, 1997; Toni, Ramnani, et al., 2001; Wolpert et al., 1998), in addition to working memory (Grover et al., 2022). Thus, it is not surprising that these regions increasingly contribute to decoding as subjects internalize the sequential task. We now include a statement reflecting these considerations in the revised Discussion.

A somewhat related point is this: when combining voxel and parcel space, a concern is whether a degree of circularity may have contributed to the improved accuracy of the combined data, because it seems to use the same MEG signals twice - the voxels most contributing are also those contributing most to a parcel being identified as relevant, as parcels reflect the average of voxels within a boundary. In this context, I struggled to understand the explanation given, ie that the improved accuracy of the hybrid model may be due to "lower spatially resolved whole-brain and higher spatially resolved regional activity patterns".

We disagree with the Reviewer’s assertion that the construction of the hybrid-space decoder is circular for the following reasons. First, the base feature set for the hybrid-space decoder constructed for all participants includes whole-brain spatial patterns of MEG source activity averaged within parcels. As stated in the manuscript, these 148 inter-parcel features reflect “lower spatially resolved whole-brain activity patterns” or global brain dynamics. We then independently test how well spatial patterns of MEG source activity for all voxels distributed within individual parcels can decode keypress actions. Again, the testing of these intra-parcel spatial patterns, intended to capture “higher spatially resolved regional brain activity patterns”, is completely independent from one another and independent from the weighting of individual inter-parcel features. These intra-parcel features could, for example, provide additional information about muscle activation patterns or the task environment. These approximately 1150 intra-parcel voxels (on average, within the total number varying between subjects) are then combined with the 148 inter-parcel features to construct the final hybrid-space decoder. In fact, this varied spatial filter approach shares some similarities to the construction of convolutional neural networks (CNNs) used to perform object recognition in image classification applications (Srinivas et al., 2016). One could also view this hybrid-space decoding approach as a spatial analogue to common timefrequency based analyses such as theta-gamma phase amplitude coupling (θ/γ PAC), which assess interactions between two or more narrow-band spectral features derived from the same time-series data (Lisman & Jensen, 2013).

We directly tested this hypothesis – that spatially overlapping intra- and inter-parcel features portray different information – by constructing an alternative hybrid-space decoder (Hybrid_Alt) that excluded average inter-parcel features which spatially overlapped with intra-parcel voxel features, and comparing the performance to the decoder used in the manuscript (Hybrid_Orig). The prediction was that if the overlapping parcel contained similar information to the more spatially resolved voxel patterns, then removing the parcel features (n=8) from the decoding analysis should not impact performance. In fact, despite making up less than 1% of the overall input feature space, removing those parcels resulted in a significant drop in overall performance greater than 2% (78.15% ± 7.03% SD for Hybrid_Orig vs. 75.49% ± 7.17% for Hybrid_Alt; Wilcoxon signed rank test, z = 3.7410, p = 1.8326e-04; Author response image 2).

Author response image 2.

Comparison of decoding performances with two different hybrid approaches. Hybrid_Alt: Intra-parcel voxel-space features of top ranked parcels and inter-parcel features of remaining parcels. Hybrid_Orig: Voxel-space features of top ranked parcels and whole-brain parcel-space features (i.e. – the version used in the manuscript). Dots represent decoding accuracy for individual subjects. Dashed lines indicate the trend in performance change across participants. Note, that Hybrid_Orig (the approach used in our manuscript) significantly outperforms the Hybrid_Alt approach, indicating that the excluded parcel features provide unique information compared to the spatially overlapping intra-parcel voxel patterns (end of figure legend).

Firstly, there will be a relatively high degree of spatial contiguity among voxels because of the nature of the signal measured, i.e. nearby individual voxels are unlikely to be independent. Secondly, the voxel data gives a somewhat misleading sense of precision; the inversion can be set up to give an estimate for each voxel, but there will not just be dependence among adjacent voxels, but also substantial variation in the sensitivity and confidence with which activity can be projected to different parts of the brain. Midline and deeper structures come to mind, where the inversion will be more problematic than for regions along the dorsal convexity of the brain, and a concern is that in those midline structures, the highest decoding accuracy is seen.

We agree with the Reviewer that some inter-parcel features representing neighboring (or spatially contiguous) voxels are likely to be correlated, an important confound in connectivity analyses (Colclough et al., 2015; Colclough et al., 2016), not performed in our investigation.

In our study, correlations between adjacent voxels effectively reduce the dimensionality of the input feature space. However, as long as there are multiple groups of correlated voxels within each parcel (i.e. – the rank is greater than 1), the intra-parcel spatial patterns could meaningfully contribute to the decoder performance, as shown by the following results:

First, we obtained higher decoding accuracy with voxel-space features (74.51% ± 7.34% SD) compared to parcel space features (68.77% ± 7.6%; Figure 3B), indicating individual voxels carry more information in decoding the keypresses than the averaged voxel-space features or parcel space features. Second, individual voxels within a parcel showed varying feature importance scores in decoding keypresses (Author response image 3). This finding shows that correlated voxels form mini subclusters that are much smaller spatially than the parcel they reside within.

Author response image 3.:

Feature importance score of individual voxels in decoding keypresses: MRMR was used to rank the individual voxel space features in decoding keypresses and the min-max normalized MRMR score was mapped to a structural brain surface. Note that individual voxels within a parcel showed different contribution to decoding (end of figure legend).

Some of these concerns could be addressed by recording head movement (with enough precision) to regress out these contributions. The authors state that head movement was monitored with 3 fiducials, and their time courses ought to provide a way to deal with this issue. The ICA procedure may not have sufficiently dealt with removing movement-related problems, but one could eg relate individual components that were identified to the keypresses as another means for checking. An alternative could be to focus on frequency ranges above the movement frequencies. The accuracy for those still seems impressive and may provide a slightly more biologically plausible assessment.

We have already addressed the issue of movement related artefacts in the first response above. With respect to a focus on frequency ranges above movement frequencies, the Reviewer states the “accuracy for those still seems impressive and may provide a slightly more biologically plausible assessment”. First, it is important to note that cortical delta-band oscillations measured with local field potentials (LFPs) in macaques is known to contain important information related to end-effector kinematics (Bansal et al., 2011; Mollazadeh et al., 2011) muscle activation patterns (Flint et al., 2012) and temporal sequencing (Churchland et al., 2012) during skilled reaching and grasping actions. Thus, there is a substantial body of evidence that low-frequency neural oscillatory activity in this range contains important information about the skill learning behavior investigated in the present study. Second, our own data shows (which the Reviewer also points out) that significant information related to the skill learning behavior is also present in higher frequency bands (see Figure 2A and Figure 3—figure supplement 1). As we pointed out in our earlier response to questions about the hybrid space decoder architecture (see above), it is likely that different, yet complimentary, information is encoded across different temporal frequencies (just as it is encoded across different spatial frequencies) (Heusser et al., 2016). Again, this interpretation is supported by our data as the highest performing classifiers in all cases (when holding all parameters constant) were always constructed from broadband input MEG data (Figure 2A and Figure 3—figure supplement 1).

One question concerns the interpretation of the results shown in Figure 4. They imply that during the course of learning, entirely different brain networks underpin the behaviour. Not only that, but they also include regions that would seem rather unexpected to be key nodes for learning and expressing relatively simple finger sequences, such as here. What then is the biological plausibility of these results? The authors seem to circumnavigate this issue by moving into a distance metric that captures the (neural network) changes over the course of learning, but the discussion seems detached from which regions are actually involved; or they offer a rather broad discussion of the anatomical regions identified here, eg in the context of LFOs, where they merely refer to "frontoparietal regions".

The Reviewer notes the shift in brain networks driving keypress decoding performance between trials 1, 11 and 36 as shown in Figure 4A. The Reviewer questions whether these shifts in brain network states underpinning the skill are biologically plausible, as well as the likelihood that bilateral superior and middle frontal and parietal cortex are important nodes within these networks.

First, previous fMRI work in humans assessed changes in functional connectivity patterns while participants performed a similar sequence learning task to our present study (Bassett et al., 2011). Using a dynamic network analysis approach, Bassett et al. showed that flexibility in the composition of individual network modules (i.e. – changes in functional brain region membership of orthogonal brain networks) is up-regulated in novel learning environments and explains differences in learning rates across individuals. Thus, consistent with our findings, it is likely that functional brain networks rapidly reconfigure during early learning of novel sequential motor skills.

Second, frontoparietal network activity is known to support motor memory encoding during early learning (Albouy et al., 2013; Albouy et al., 2012). For example, reactivation events in the posterior parietal (Qin et al., 1997) and medial prefrontal (Euston et al., 2007; Molle & Born, 2009) cortex (MPFC) have been temporally linked to hippocampal replay, and are posited to support memory consolidation across several memory domains (Frankland & Bontempi, 2005), including motor sequence learning (Albouy et al., 2015; Buch et al., 2021; F. Jacobacci et al., 2020). Further, synchronized interactions between MPFC and hippocampus are more prominent during early as opposed to later learning stages (Albouy et al., 2013; Gais et al., 2007; Sterpenich et al., 2009), perhaps reflecting “redistribution of hippocampal memories to MPFC” (Albouy et al., 2013). MPFC contributes to very early memory formation by learning association between contexts, locations, events and adaptive responses during rapid learning (Euston et al., 2012). Consistently, coupling between hippocampus and MPFC has been shown during initial memory encoding and during subsequent rest (van Kesteren et al., 2010; van Kesteren et al., 2012). Importantly, MPFC activity during initial memory encoding predicts subsequent recall (Wagner et al., 1998). Thus, the spatial map required to encode a motor sequence memory may be “built under the supervision of the prefrontal cortex” (Albouy et al., 2012), also engaged in the development of an abstract representation of the sequence (Ashe et al., 2006). In more abstract terms, the prefrontal, premotor and parietal cortices support novice performance “by deploying attentional and control processes” (Doyon et al., 2009; Hikosaka et al., 2002; Penhune & Steele, 2012) required during early learning (Doyon et al., 2009; Hikosaka et al., 2002; Penhune & Steele, 2012). The dorsolateral prefrontal cortex DLPFC specifically is thought to engage in goal selection and sequence monitoring during early skill practice (Schendan et al., 2003), all consistent with the schema model of declarative memory in which prefrontal cortices play an important role in encoding (Morris, 2006; Tse et al., 2007). Thus, several prefrontal and frontoparietal regions contributing to long term learning (Berlot et al., 2020) are also engaged in early stages of encoding. Altogether, there is strong biological support for the involvement of bilateral prefrontal and frontoparietal regions to decoding during early skill learning. We now address this issue in the revised manuscript.

If I understand correctly, the offline neural representation analysis is in essence the comparison of the last keypress vs the first keypress of the next sequence. In that sense, the activity during offline rest periods is actually not considered. This makes the nomenclature somewhat confusing. While it matches the behavioural analysis, having only key presses one can't do it in any other way, but here the authors actually do have recordings of brain activity during offline rest. So at the very least calling it offline neural representation is misleading to this reviewer because what is compared is activity during the last and during the next keypress, not activity during offline periods. But it also seems a missed opportunity - the authors argue that most of the relevant learning occurs during offline rest periods, yet there is no attempt to actually test whether activity during this period can be useful for the questions at hand here.

We agree with the Reviewer that our previous “offline neural representation” nomenclature could be misinterpreted. In the revised manuscript we refer to this difference as the “offline neural representational change”. Please, note that our previous work did link offline neural activity (i.e. – 16-22 Hz beta power (Bonstrup et al., 2019) and neural replay density (Buch et al., 2021) during inter-practice rest periods) to observed micro-offline gains.

Reviewer #2 (Public review):

Summary

Dash et al. asked whether and how the neural representation of individual finger movements is "contextualized" within a trained sequence during the very early period of sequential skill learning by using decoding of MEG signal. Specifically, they assessed whether/how the same finger presses (pressing index finger) embedded in the different ordinal positions of a practiced sequence (4-1-3-2-4; here, the numbers 1 through 4 correspond to the little through the index fingers of the non-dominant left hand) change their representation (MEG feature). They did this by computing either the decoding accuracy of the index finger at the ordinal positions 1 vs. 5 (index_OP1 vs index_OP5) or pattern distance between index_OP1 vs. index_OP5 at each training trial and found that both the decoding accuracy and the pattern distance progressively increase over the course of learning trials. More interestingly, they also computed the pattern distance for index_OP5 for the last execution of a practice trial vs. index_OP1 for the first execution in the next practice trial (i.e., across the rest period). This "off-line" distance was significantly larger than the "on-line" distance, which was computed within practice trials and predicted micro-offline skill gain. Based on these results, the authors conclude that the differentiation of representation for the identical movement embedded in different positions of a sequential skill ("contextualization") primarily occurs during early skill learning, especially during rest, consistent with the recent theory of the "micro-offline learning" proposed by the authors' group. I think this is an important and timely topic for the field of motor learning and beyond.

Strengths

The specific strengths of the current work are as follows. First, the use of temporally rich neural information (MEG signal) has a large advantage over previous studies testing sequential representations using fMRI. This allowed the authors to examine the earliest period (= the first few minutes of training) of skill learning with finer temporal resolution. Second, through the optimization of MEG feature extraction, the current study achieved extremely high decoding accuracy (approx. 94%) compared to previous works. As claimed by the authors, this is one of the strengths of the paper (but see my comments). Third, although some potential refinement might be needed, comparing "online" and "offline" pattern distance is a neat idea.

Weaknesses

Along with the strengths I raised above, the paper has some weaknesses. First, the pursuit of high decoding accuracy, especially the choice of time points and window length (i.e., 200 msec window starting from 0 msec from key press onset), casts a shadow on the interpretation of the main result. Currently, it is unclear whether the decoding results simply reflect behavioral change or true underlying neural change. As shown in the behavioral data, the key press speed reached 3~4 presses per second already at around the end of the early learning period (11th trial), which means inter-press intervals become as short as 250-330 msec. Thus, in almost more than 60% of training period data, the time window for MEG feature extraction (200 msec) spans around 60% of the inter-press intervals. Considering that the preparation/cueing of subsequent presses starts ahead of the actual press (e.g., Kornysheva et al., 2019) and/or potential online planning (e.g., Ariani and Diedrichsen, 2019), the decoder likely has captured these future press information as well as the signal related to the current key press, independent of the formation of genuine sequential representation (e.g., "contextualization" of individual press). This may also explain the gradual increase in decoding accuracy or pattern distance between index_OP1 vs. index_OP5 (Figure 4C and 5A), which co-occurred with performance improvement, as shorter inter-press intervals are more favorable for the dissociating the two index finger presses followed by different finger presses. The compromised decoding accuracies for the control sequences can be explained in similar logic. Therefore, more careful consideration and elaborated discussion seem necessary when trying to both achieve high-performance decoding and assess early skill learning, as it can impact all the subsequent analyses.

The Reviewer raises the possibility that (given the windowing parameters used in the present study) an increase in “contextualization” with learning could simply reflect faster typing speeds as opposed to an actual change in the underlying neural representation.

We now include a new control analysis that addresses this issue as well as additional re-examination of previously reported results with respect to this issue – all of which are inconsistent with this alternative explanation that “contextualization” reflects a change in mixing of keypress related MEG features as opposed to a change in the underlying representations themselves. As correct sequences are generated at higher and higher speeds over training, MEG activity patterns related to the planning, execution, evaluation and memory of individual keypresses overlap more in time. Thus, increased overlap between the “4” and “1” keypresses (at the start of the sequence) and “2” and “4” keypresses (at the end of the sequence) could artefactually increase contextualization distances even if the underlying neural representations for the individual keypresses remain unchanged. One must also keep in mind that since participants repeat the sequence multiple times within the same trial, a majority of the index finger keypresses are performed adjacent to one another (i.e. - the “4-4” transition marking the end of one sequence and the beginning of the next). Thus, increased overlap between consecutive index finger keypresses as typing speed increased should increase their similarity and mask contextualization related changes to the underlying neural representations.

We addressed this question by conducting a new multivariate regression analysis to directly assess whether the neural representation distance score could be predicted by the 4-1, 2-4 and 4-4 keypress transition times observed for each complete correct sequence (both predictor and response variables were z-score normalized within-subject). The results of this analysis also affirmed that the possible alternative explanation that contextualization effects are simple reflections of increased mixing is not supported by the data (Adjusted R² = 0.00431; F = 5.62). We now include this new negative control analysis in the revised manuscript.

We also re-examined our previously reported classification results with respect to this issue. We reasoned that if mixing effects reflecting the ordinal sequence structure is an important driver of the contextualization finding, these effects should be observable in the distribution of decoder misclassifications. For example, “4” keypresses would be more likely to be misclassified as “1” or “2” keypresses (or vice versa) than as “3” keypresses. The confusion matrices presented in Figures 3C and 4B and Figure 3—figure supplement 3A display a distribution of misclassifications that is inconsistent with an alternative mixing effect explanation of contextualization.

Based upon the increased overlap between adjacent index finger keypresses (i.e. – “4-4” transition), we also reasoned that the decoder tasked with separating individual index finger keypresses into two distinct classes based upon sequence position, should show decreased performance as typing speed increases. However, Figure 4C in our manuscript shows that this is not the case. The 2-class hybrid classifier actually displays improved classification performance over early practice trials despite greater temporal overlap. Again, this is inconsistent with the idea that the contextualization effect simply reflects increased mixing of individual keypress features.

In summary, both re-examination of previously reported data and new control analyses all converged on the idea that the proximity between keypresses does not explain contextualization.

We do agree with the Reviewer that the naturalistic, generative, self-paced task employed in the present study results in overlapping brain processes related to planning, execution, evaluation and memory of the action sequence. We also agree that there are several tradeoffs to consider in the construction of the classifiers depending on the study aim. Given our aim of optimizing keypress decoder accuracy in the present study, the set of trade-offs resulted in representations reflecting more the latter three processes, and less so the planning component. Whether separate decoders can be constructed to tease apart the representations or networks supporting these overlapping processes is an important future direction of research in this area. For example, work presently underway in our lab constrains the selection of windowing parameters in a manner that allows individual classifiers to be temporally linked to specific planning, execution, evaluation or memory-related processes to discern which brain networks are involved and how they adaptively reorganize with learning. Results from the present study (Figure 4—figure supplement 2) showing hybrid-space decoder prediction accuracies exceeding 74% for temporal windows spanning as little as 25ms and located up to 100ms prior to the KeyDown event strongly support the feasibility of such an approach.

Related to the above point, testing only one particular sequence (4-1-3-2-4), aside from the control ones, limits the generalizability of the finding. This also may have contributed to the extremely high decoding accuracy reported in the current study.

The Reviewer raises a question about the generalizability of the decoder accuracy reported in our study. Fortunately, a comparison between decoder performances on Day 1 and Day 2 datasets does provide insight into this issue. As the Reviewer points out, the classifiers in this study were trained and tested on keypresses performed while practicing a specific sequence (4-1-3-2-4). The study was designed this way as to avoid the impact of interference effects on learning dynamics. The cross-validated performance of classifiers on MEG data collected within the same session was 90.47% overall accuracy (4-class; Figure 3C). We then tested classifier performance on data collected during a separate MEG session conducted approximately 24 hours later (Day 2; see Figure 3 — figure supplement 3). We observed a reduction in overall accuracy rate to 87.11% when tested on MEG data recorded while participants performed the same learned sequence, and 79.44% when they performed several previously unpracticed sequences. Both changes in accuracy are important with regards to the generalizability of our findings. First, 87.11% performance accuracy for the trained sequence data on Day 2 (a reduction of only 3.36%) indicates that the hybrid-space decoder performance is robust over multiple MEG sessions, and thus, robust to variations in SNR across the MEG sensor array caused by small differences in head position between scans. This indicates a substantial advantage over sensor-space decoding approaches. Furthermore, when tested on data from unpracticed sequences, overall performance dropped an additional 7.67%. This difference reflects the performance bias of the classifier for the trained sequence, possibly caused by high-order sequence structure being incorporated into the feature weights. In the future, it will be important to understand in more detail how random or repeated keypress sequence training data impacts overall decoder performance and generalization. We strongly agree with the Reviewer that the issue of generalizability is extremely important and have added a new paragraph to the Discussion in the revised manuscript highlighting the strengths and weaknesses of our study with respect to this issue.

In terms of clinical BCI, one of the potential relevance of the study, as claimed by the authors, it is not clear that the specific time window chosen in the current study (up to 200 msec since key press onset) is really useful. In most cases, clinical BCI would target neural signals with no overt movement execution due to patients' inability to move (e.g., Hochberg et al., 2012). Given the time window, the surprisingly high performance of the current decoder may result from sensory feedback and/or planning of subsequent movement, which may not always be available in the clinical BCI context. Of course, the decoding accuracy is still much higher than chance even when using signal before the key press (as shown in Figure 4 Supplement 2), but it is not immediately clear to me that the authors relate their high decoding accuracy based on post-movement signal to clinical BCI settings.

The Reviewer questions the relevance of the specific window parameters used in the present study for clinical BCI applications, particularly for paretic patients who are unable to produce finger movements or for whom afferent sensory feedback is no longer intact. We strongly agree with the Reviewer that any intended clinical application must carefully consider the specific input feature constraints dictated by the clinical cohort, and in turn impose appropriate and complimentary constraints on classifier parameters that may differ from the ones used in the present study. We now highlight this issue in the Discussion of the revised manuscript and relate our present findings to published clinical BCI work within this context.

One of the important and fascinating claims of the current study is that the "contextualization" of individual finger movements in a trained sequence specifically occurs during short rest periods in very early skill learning, echoing the recent theory of micro-offline learning proposed by the authors' group. Here, I think two points need to be clarified. First, the concept of "contextualization" is kept somewhat blurry throughout the text. It is only at the later part of the Discussion (around line #330 on page 13) that some potential mechanism for the "contextualization" is provided as "what-and-where" binding. Still, it is unclear what "contextualization" actually is in the current data, as the MEG signal analyzed is extracted from 0-200 msec after the keypress. If one thinks something is contextualizing an action, that contextualization should come earlier than the action itself.

The Reviewer requests that we: 1) more clearly define our use of the term “contextualization” and 2) provide the rationale for assessing it over a 200ms window aligned to the KeyDown event. This choice of window parameters means that the MEG activity used in our analysis was coincident with, rather than preceding, the actual keypresses. We define contextualization as the differentiation of representation for the identical movement embedded in different positions of a sequential skill. That is, representations of individual action elements progressively incorporate information about their relationship to the overall sequence structure as the skill is learned. We agree with the Reviewer that this can be appropriately interpreted as “what-and-where” binding. We now incorporate this definition in the Introduction of the revised manuscript as requested.

The window parameters for optimizing accurate decoding individual finger movements were determined using a grid search of the parameter space (a sliding window of variable width between 25-350 ms with 25 ms increments variably aligned from 0 to +100ms with 10ms increments relative to the KeyDown event). This approach generated 140 different temporal windows for each keypress for each participant, with the final parameter selection determined through comparison of the resulting performance between each decoder. Importantly, the decision to optimize for decoding accuracy placed an emphasis on keypress representations characterized by the most consistent and robust features shared across subjects, which in turn maximize statistical power in detecting common learning-related changes. In this case, the optimal window encompassed a 200ms epoch aligned to the KeyDown event (t₀ = 0 ms). We then asked if the representations (i.e. – spatial patterns of combined parcel- and voxel-space activity) of the same digit at two different sequence positions changed with practice within this optimal decoding window. Of course, our findings do not rule out the possibility that contextualization can also be found before or even after this time window, as we did not directly address this issue in the present study. Future work in our lab, as pointed out above, are investigating contextualization within different time windows tailored specifically for assessing sequence skill action planning, execution, evaluation and memory processes.

The second point is that the result provided by the authors is not yet convincing enough to support the claim that "contextualization" occurs during rest. In the original analysis, the authors presented the statistical significance regarding the correlation between the "offline" pattern differentiation and micro-offline skill gain (Figure 5. Supplement 1), as well as the larger "offline" distance than "online" distance (Figure 5B). However, this analysis looks like regressing two variables (monotonically) increasing as a function of the trial. Although some information in this analysis, such as what the independent/dependent variables were or how individual subjects were treated, was missing in the Methods, getting a statistically significant slope seems unsurprising in such a situation. Also, curiously, the same quantitative evidence was not provided for its "online" counterpart, and the authors only briefly mentioned in the text that there was no significant correlation between them. It may be true looking at the data in Figure 5A as the online representation distance looks less monotonically changing, but the classification accuracy presented in Figure 4C, which should reflect similar representational distance, shows a more monotonic increase up to the 11th trial. Further, the ways the "online" and "offline" representation distance was estimated seem to make them not directly comparable. While the "online" distance was computed using all the correct press data within each 10 sec of execution, the "offline" distance is basically computed by only two presses (i.e., the last index_OP5 vs. the first index_OP1 separated by 10 sec of rest). Theoretically, the distance between the neural activity patterns for temporally closer events tends to be closer than that between the patterns for temporally far-apart events. It would be fairer to use the distance between the first index_OP1 vs. the last index_OP5 within an execution period for "online" distance, as well.

The Reviewer suggests that the current data is not enough to show that contextualization occurs during rest and raises two important concerns: 1) the relationship between online contextualization and micro-online gains is not shown, and 2) the online distance was calculated differently from its offline counterpart (i.e. - instead of calculating the distance between last Index_OP5 and first Index_OP1 from a single trial, the distance was calculated for each sequence within a trial and then averaged).

We addressed the first concern by performing individual subject correlations between 1) contextualization changes during rest intervals and micro-offline gains; 2) contextualization changes during practice trials and micro-online gains, and 3) contextualization changes during practice trials and micro-offline gains (Figure 5 – figure supplement 4). We then statistically compared the resulting correlation coefficient distributions and found that within-subject correlations for contextualization changes during rest intervals and micro-offline gains were significantly higher than online contextualization and micro-online gains (t = 3.2827, p = 0.0015) and online contextualization and micro-offline gains (t = 3.7021, p = 5.3013e-04). These results are consistent with our interpretation that micro-offline gains are supported by contextualization changes during the inter-practice rest periods.

With respect to the second concern, we agree with the Reviewer that one limitation of the analysis comparing online versus offline changes in contextualization as presented in the original manuscript, is that it does not eliminate the possibility that any differences could simply be explained by the passage of time (which is smaller for the online analysis compared to the offline analysis). The Reviewer suggests an approach that addresses this issue, which we have now carried out. When quantifying online changes in contextualization from the first Index_OP1 the last Index_OP5 keypress in the same trial we observed no learning-related trend (Figure 5 – figure supplement 5, right panel). Importantly, offline distances were significantly larger than online distances regardless of the measurement approach and neither predicted online learning (Figure 5 – figure supplement 6).

A related concern regarding the control analysis, where individual values for max speed and the degree of online contextualization were compared (Figure 5 Supplement 3), is whether the individual difference is meaningful. If I understood correctly, the optimization of the decoding process (temporal window, feature inclusion/reduction, decoder, etc.) was performed for individual participants, and the same feature extraction was also employed for the analysis of representation distance (i.e., contextualization). If this is the case, the distances are individually differently calculated and they may need to be normalized relative to some stable reference (e.g., 1 vs. 4 or average distance within the control sequence presses) before comparison across the individuals.

The Reviewer makes a good point here. We have now implemented the suggested normalization procedure in the analysis provided in the revised manuscript.

Reviewer #3 (Public review):

Summary:

One goal of this paper is to introduce a new approach for highly accurate decoding of finger movements from human magnetoencephalography data via dimension reduction of a "multiscale, hybrid" feature space. Following this decoding approach, the authors aim to show that early skill learning involves "contextualization" of the neural coding of individual movements, relative to their position in a sequence of consecutive movements. Furthermore, they aim to show that this "contextualization" develops primarily during short rest periods interspersed with skill training and correlates with a performance metric which the authors interpret as an indicator of offline learning.

Strengths:

A clear strength of the paper is the innovative decoding approach, which achieves impressive decoding accuracies via dimension reduction of a "multi-scale, hybrid space". This hybrid-space approach follows the neurobiologically plausible idea of the concurrent distribution of neural coding across local circuits as well as large-scale networks. A further strength of the study is the large number of tested dimension reduction techniques and classifiers (though the manuscript reveals little about the comparison of the latter).

We appreciate the Reviewer’s comments regarding the paper’s strengths.

A simple control analysis based on shuffled class labels could lend further support to this complex decoding approach. As a control analysis that completely rules out any source of overfitting, the authors could test the decoder after shuffling class labels. Following such shuffling, decoding accuracies should drop to chance level for all decoding approaches, including the optimized decoder. This would also provide an estimate of actual chance-level performance (which is informative over and beyond the theoretical chance level). Furthermore, currently, the manuscript does not explain the huge drop in decoding accuracies for the voxel-space decoding (Figure 3B). Finally, the authors' approach to cortical parcellation raises questions regarding the information carried by varying dipole orientations within a parcel (which currently seems to be ignored?) and the implementation of the mean-flipping method (given that there are two dimensions - space and time - what do the authors refer to when they talk about the sign of the "average source", line 477?).

The Reviewer recommends that we: 1) conduct an additional control analysis on classifier performance using shuffled class labels, 2) provide a more detailed explanation regarding the drop in decoding accuracies for the voxel-space decoding following LDA dimensionality reduction (see Fig 3B), and 3) provide additional details on how problems related to dipole solution orientations were addressed in the present study.

In relation to the first point, we have now implemented a random shuffling approach as a control for the classification analyses. The results of this analysis indicated that the chance level accuracy was 22.12% (± SD 9.1%) for individual keypress decoding (4-class classification), and 18.41% (± SD 7.4%) for individual sequence item decoding (5-class classification), irrespective of the input feature set or the type of decoder used. Thus, the decoding accuracy observed with the final model was substantially higher than these chance levels.

Second, please note that the dimensionality of the voxel-space feature set is very high (i.e. – 15684). LDA attempts to map the input features onto a much smaller dimensional space (number of classes – 1; e.g. – 3 dimensions, for 4-class keypress decoding). Given the very high dimension of the voxel-space input features in this case, the resulting mapping exhibits reduced accuracy. Despite this general consideration, please refer to Figure 3—figure supplement 3, where we observe improvement in voxel-space decoder performance when utilizing alternative dimensionality reduction techniques.

The decoders constructed in the present study assess the average spatial patterns across time (as defined by the windowing procedure) in the input feature space. We now provide additional details in the Methods of the revised manuscript pertaining to the parcellation procedure and how the sign ambiguity problem was addressed in our analysis.

Weaknesses:

A clear weakness of the paper lies in the authors' conclusions regarding "contextualization". Several potential confounds, described below, question the neurobiological implications proposed by the authors and provide a simpler explanation of the results. Furthermore, the paper follows the assumption that short breaks result in offline skill learning, while recent evidence, described below, casts doubt on this assumption.

We thank the Reviewer for giving us the opportunity to address these issues in detail (see below).

The authors interpret the ordinal position information captured by their decoding approach as a reflection of neural coding dedicated to the local context of a movement (Figure 4). One way to dissociate ordinal position information from information about the moving effectors is to train a classifier on one sequence and test the classifier on other sequences that require the same movements, but in different positions (Kornysheva et al., 2019). In the present study, however, participants trained to repeat a single sequence (4-1-3-2-4). As a result, ordinal position information is potentially confounded by the fixed finger transitions around each of the two critical positions (first and fifth press). Across consecutive correct sequences, the first keypress in a given sequence was always preceded by a movement of the index finger (=last movement of the preceding sequence), and followed by a little finger movement. The last keypress, on the other hand, was always preceded by a ring finger movement, and followed by an index finger movement (=first movement of the next sequence). Figure 4 - Supplement 2 shows that finger identity can be decoded with high accuracy (>70%) across a large time window around the time of the key press, up to at least +/-100 ms (and likely beyond, given that decoding accuracy is still high at the boundaries of the window depicted in that figure). This time window approaches the keypress transition times in this study. Given that distinct finger transitions characterized the first and fifth keypress, the classifier could thus rely on persistent (or "lingering") information from the preceding finger movement, and/or "preparatory" information about the subsequent finger movement, in order to dissociate the first and fifth keypress. Currently, the manuscript provides no evidence that the context information captured by the decoding approach is more than a by-product of temporally extended, and therefore overlapping, but independent neural representations of consecutive keypresses that are executed in close temporal proximity - rather than a neural representation dedicated to context.

Such temporal overlap of consecutive, independent finger representations may also account for the dynamics of "ordinal coding"/"contextualization", i.e., the increase in 2-class decoding accuracy, across Day 1 (Figure 4C). As learning progresses, both tapping speed and the consistency of keypress transition times increase (Figure 1), i.e., consecutive keypresses are closer in time, and more consistently so. As a result, information related to a given keypress is increasingly overlapping in time with information related to the preceding and subsequent keypresses. The authors seem to argue that their regression analysis in Figure 5 - Figure Supplement 3 speaks against any influence of tapping speed on "ordinal coding" (even though that argument is not made explicitly in the manuscript). However, Figure 5 - Figure Supplement 3 shows inter-individual differences in a between-subject analysis (across trials, as in panel A, or separately for each trial, as in panel B), and, therefore, says little about the within-subject dynamics of "ordinal coding" across the experiment. A regression of trial-by-trial "ordinal coding" on trial-by-trial tapping speed (either within-subject or at a group-level, after averaging across subjects) could address this issue. Given the highly similar dynamics of "ordinal coding" on the one hand (Figure 4C), and tapping speed on the other hand (Figure 1B), I would expect a strong relationship between the two in the suggested within-subject (or group-level) regression. Furthermore, learning should increase the number of (consecutively) correct sequences, and, thus, the consistency of finger transitions. Therefore, the increase in 2-class decoding accuracy may simply reflect an increasing overlap in time of increasingly consistent information from consecutive keypresses, which allows the classifier to dissociate the first and fifth keypress more reliably as learning progresses, simply based on the characteristic finger transitions associated with each. In other words, given that the physical context of a given keypress changes as learning progresses - keypresses move closer together in time and are more consistently correct - it seems problematic to conclude that the mental representation of that context changes. To draw that conclusion, the physical context should remain stable (or any changes to the physical context should be controlled for).

The issues raised by Reviewer #3 here are similar to two issues raised by Reviewer #2 above. We agree they must both be carefully considered in any evaluation of our findings.

As both Reviewers pointed out, the classifiers in this study were trained and tested on keypresses performed while practicing a specific sequence (4-1-3-2-4). The study was designed this way as to avoid the impact of interference effects on learning dynamics. The cross-validated performance of classifiers on MEG data collected within the same session was 90.47% overall accuracy (4class; Figure 3C). We then tested classifier performance on data collected during a separate MEG session conducted approximately 24 hours later (Day 2; see Figure 3—supplement 3). We observed a reduction in overall accuracy rate to 87.11% when tested on MEG data recorded while participants performed the same learned sequence, and 79.44% when they performed several previously unpracticed sequences. This classification performance difference of 7.67% when tested on the Day 2 data could reflect the performance bias of the classifier for the trained sequence, possibly caused by mixed information from temporally close keypresses being incorporated into the feature weights.

Along these same lines, both Reviewers also raise the possibility that an increase in “ordinal coding/contextualization” with learning could simply reflect an increase in this mixing effect caused by faster typing speeds as opposed to an actual change in the underlying neural representation. The basic idea is that as correct sequences are generated at higher and higher speeds over training, MEG activity patterns related to the planning, execution, evaluation and memory of individual keypresses overlap more in time. Thus, increased overlap between the “4” and “1” keypresses (at the start of the sequence) and “2” and “4” keypresses (at the end of the sequence) could artefactually increase contextualization distances even if the underlying neural representations for the individual keypresses remain unchanged (assuming this mixing of representations is used by the classifier to differentially tag each index finger press). If this were the case, it follows that such mixing effects reflecting the ordinal sequence structure would also be observable in the distribution of decoder misclassifications. For example, “4” keypresses would be more likely to be misclassified as “1” or “2” keypresses (or vice versa) than as “3” keypresses. The confusion matrices presented in Figures 3C and 4B and Figure 3—figure supplement 3A in the previously submitted manuscript do not show this trend in the distribution of misclassifications across the four fingers.

Following this logic, it’s also possible that if the ordinal coding is largely driven by this mixing effect, the increased overlap between consecutive index finger keypresses during the 4-4 transition marking the end of one sequence and the beginning of the next one could actually mask contextualization-related changes to the underlying neural representations and make them harder to detect. In this case, a decoder tasked with separating individual index finger keypresses into two distinct classes based upon sequence position might show decreased performance with learning as adjacent keypresses overlapped in time with each other to an increasing extent. However, Figure 4C in our previously submitted manuscript does not support this possibility, as the 2-class hybrid classifier displays improved classification performance over early practice trials despite greater temporal overlap.

As noted in the above reply to Reviewer #2, we also conducted a new multivariate regression analysis to directly assess whether the neural representation distance score could be predicted by the 4-1, 2-4 and 4-4 keypress transition times observed for each complete correct sequence (both predictor and response variables were z-score normalized within-subject). The results of this analysis affirmed that the possible alternative explanation put forward by the Reviewer is not supported by our data (Adjusted R² = 0.00431; F = 5.62). We now include this new negative control analysis result in the revised manuscript.

Finally, the Reviewer hints that one way to address this issue would be to compare MEG responses before and after learning for sequences typed at a fixed speed. However, given that the speed-accuracy trade-off should improve with learning, a comparison between unlearned and learned skill states would dictate that the skill be evaluated at a very low fixed speed. Essentially, such a design presents the problem that the post-training test is evaluating the representation in the unlearned behavioral state that is not representative of the acquired skill. Thus, this approach would miss most learning effects on a task in which speed is the main learning metrics.

A similar difference in physical context may explain why neural representation distances ("differentiation") differ between rest and practice (Figure 5). The authors define "offline differentiation" by comparing the hybrid space features of the last index finger movement of a trial (ordinal position 5) and the first index finger movement of the next trial (ordinal position 1). However, the latter is not only the first movement in the sequence but also the very first movement in that trial (at least in trials that started with a correct sequence), i.e., not preceded by any recent movement. In contrast, the last index finger of the last correct sequence in the preceding trial includes the characteristic finger transition from the fourth to the fifth movement. Thus, there is more overlapping information arising from the consistent, neighbouring keypresses for the last index finger movement, compared to the first index finger movement of the next trial. A strong difference (larger neural representation distance) between these two movements is, therefore, not surprising, given the task design, and this difference is also expected to increase with learning, given the increase in tapping speed, and the consequent stronger overlap in representations for consecutive keypresses. Furthermore, initiating a new sequence involves pre-planning, while ongoing practice relies on online planning (Ariani et al., eNeuro 2021), i.e., two mental operations that are dissociable at the level of neural representation (Ariani et al., bioRxiv 2023).

The Reviewer argues that the comparison of last finger movement of a trial and the first in the next trial are performed in different circumstances and contexts. This is an important point and one we tend to agree with. For this task, the first sequence in a practice trial is pre-planned before the first keypress is performed. This occurs in a somewhat different context from the sequence iterations that follow, which involve temporally overlapping planning, execution and evaluation processes. The Reviewer is concerned about a difference in the temporal mixing effect issue raised above between the first and last keypresses performed in a trial. Please, note that since neural representations of individual actions are competitively queued during the pre-planning period in a manner that reflects the ordinal structure of the learned sequence (Kornysheva et al., 2019), mixing effects are most likely present also for the first keypress in a trial.

Separately, the Reviewer suggests that contextualization during early learning may reflect preplanning or online planning. This is an interesting proposal. Given the decoding time-window used in this investigation, we cannot dissect separate contributions of planning, memory and sensory feedback to contextualization. Taking advantage of the superior temporal resolution of MEG relative to fMRI tools, work under way in our lab is investigating decoding time-windows more appropriate to address each of these questions.

Given these differences in the physical context and associated mental processes, it is not surprising that "offline differentiation", as defined here, is more pronounced than "online differentiation". For the latter, the authors compared movements that were better matched regarding the presence of consistent preceding and subsequent keypresses (online differentiation was defined as the mean difference between all first vs. last index finger movements during practice). It is unclear why the authors did not follow a similar definition for "online differentiation" as for "micro-online gains" (and, indeed, a definition that is more consistent with their definition of "offline differentiation"), i.e., the difference between the first index finger movement of the first correct sequence during practice, and the last index finger of the last correct sequence. While these two movements are, again, not matched for the presence of neighbouring keypresses (see the argument above), this mismatch would at least be the same across "offline differentiation" and "online differentiation", so they would be more comparable.

This is the same point made earlier by Reviewer #2, and we agree with this assessment. As stated in the response to Reviewer #2 above, we have now carried out quantification of online contextualization using this approach and included it in the revised manuscript. We thank the Reviewer for this suggestion.

A further complication in interpreting the results regarding "contextualization" stems from the visual feedback that participants received during the task. Each keypress generated an asterisk shown above the string on the screen, irrespective of whether the keypress was correct or incorrect. As a result, incorrect (e.g., additional, or missing) keypresses could shift the phase of the visual feedback string (of asterisks) relative to the ordinal position of the current movement in the sequence (e.g., the fifth movement in the sequence could coincide with the presentation of any asterisk in the string, from the first to the fifth). Given that more incorrect keypresses are expected at the start of the experiment, compared to later stages, the consistency in visual feedback position, relative to the ordinal position of the movement in the sequence, increased across the experiment. A better differentiation between the first and the fifth movement with learning could, therefore, simply reflect better decoding of the more consistent visual feedback, based either on the feedback-induced brain response, or feedback-induced eye movements (the study did not include eye tracking). It is not clear why the authors introduced this complicated visual feedback in their task, besides consistency with their previous studies.

We strongly agree with the Reviewer that eye movements related to task engagement are important to rule out as a potential driver of the decoding accuracy or contextualizaton effect. We address this issue above in response to a question raised by Reviewer #1 about the impact of movement related artefacts on our findings.

First, the assumption the Reviewer makes here about the distribution of errors in this task is incorrect. On average across subjects, 2.32% ± 1.48% (mean ± SD) of all keypresses performed were errors, which were evenly distributed across the four possible keypress responses. While errors increased progressively over practice trials, they did so in proportion to the increase in correct keypresses, so that the overall ratio of correct-to-incorrect keypresses remained stable over the training session. Thus, the Reviewer’s assumptions that there is a higher relative frequency of errors in early trials, and a resulting systematic trend phase shift differences between the visual display updates (i.e. – a change in asterisk position above the displayed sequence) and the keypress performed is not substantiated by the data. To the contrary, the asterisk position on the display and the keypress being executed remained highly correlated over the entire training session. We now include a statement about the frequency and distribution of errors in the revised manuscript.

Given this high correlation, we firmly agree with the Reviewer that the issue of eye movement related artefacts is still an important one to address. Fortunately, we did collect eye movement data during the MEG recordings so were able to investigate this. As detailed in the response to Reviewer #1 above, we found that gaze positions and eye-movement velocity time-locked to visual display updates (i.e. – a change in asterisk position above the displayed sequence) did not reflect the asterisk location above chance levels (Overall cross-validated accuracy = 0.21817; see Author response image 1). Furthermore, an inspection of the eye position data revealed that most participants on most trials displayed random walk gaze patterns around a center fixation point, indicating that participants did not attend to the asterisk position on the display. This is consistent with intrinsic generation of the action sequence, and congruent with the fact that the display does not provide explicit feedback related to performance. As pointed out above, a similar real-world example would be manually inputting a long password into a secure online application. In this case, one intrinsically generates the sequence from memory and receives similar feedback about the password sequence position (also provided as asterisks), which is typically ignored by the user.

The minimal participant engagement with the visual display in this explicit sequence learning motor task (which is highly generative in nature) contrasts markedly with behavior observed when reactive responses to stimulus cues are needed in the serial reaction time task (SRTT). This is a crucial difference that must be carefully considered when comparing findings across studies using the two sequence learning tasks.

The authors report a significant correlation between "offline differentiation" and cumulative microoffline gains. However, it would be more informative to correlate trial-by-trial changes in each of the two variables. This would address the question of whether there is a trial-by-trial relation between the degree of "contextualization" and the amount of micro-offline gains - are performance changes (micro-offline gains) less pronounced across rest periods for which the change in "contextualization" is relatively low? Furthermore, is the relationship between micro-offline gains and "offline differentiation" significantly stronger than the relationship between micro-offline gains and "online differentiation"?

In response to a similar issue raised above by Reviewer #2, we now include new analyses comparing correlation magnitudes between (1) “online differentiation” vs micro-online gains, (2) “online differentiation” vs micro-offline gains and (3) “offline differentiation” and micro-offline gains (see Figure 5 – figure supplement  4, 5 and 6). These new analyses and results have been added to the revised manuscript. Once again, we thank both Reviewers for this suggestion.

The authors follow the assumption that micro-offline gains reflect offline learning.

We disagree with this statement. The original (Bonstrup et al., 2019) paper clearly states that micro-offline gains do not necessarily reflect offline learning in some cases and must be carefully interpreted based upon the behavioral context within which they are observed. Further, the paper lays out the conditions under which one can have confidence that micro-offline gains reflect offline learning. In fact, the excellent meta-analysis of (Pan & Rickard, 2015), which re-interprets the benefits of sleep in overnight skill consolidation from a “reactive inhibition” perspective, was a crucial resource in the experimental design of our initial study (Bonstrup et al., 2019), as well as in all our subsequent work. Pan & Rickard state:

“Empirically, reactive inhibition refers to performance worsening that can accumulate during a period of continuous training (Hull, 1943 . It tends to dissipate, at least in part, when brief breaks are inserted between blocks of training. If there are multiple performance-break cycles over a training session, as in the motor sequence literature, performance can exhibit a scalloped effect, worsening during each uninterrupted performance block but improving across blocks(Brawn et al., 2010; Rickard et al., 2008 . Rickard, Cai, Rieth, Jones, and Ard (2008 and Brawn, Fenn, Nusbaum, and Margoliash (2010 (Brawn et al., 2010; Rickard et al., 2008 demonstrated highly robust scalloped reactive inhibition effects using the commonly employed 30 s–30 s performance break cycle, as shown for Rickard et al.’s (2008 massed practice sleep group in Figure 2. The scalloped effect is evident for that group after the first few 30 s blocks of each session. The absence of the scalloped effect during the first few blocks of training in the massed group suggests that rapid learning during that period masks any reactive inhibition effect.”

Crucially, Pan & Rickard make several concrete recommendations for reducing the impact of the reactive inhibition confound on offline learning studies. One of these recommendations was to reduce practice times to 10s (most prior sequence learning studies up until that point had employed 30s long practice trials). They state:

“The traditional design involving 30 s-30 s performance break cycles should be abandoned given the evidence that it results in a reactive inhibition confound, and alternative designs with reduced performance duration per block used instead (Pan & Rickard, 2015 . One promising possibility is to switch to 10 s performance durations for each performance-break cycle Instead (Pan & Rickard, 2015 . That design appears sufficient to eliminate at least the majority of the reactive inhibition effect (Brawn et al., 2010; Rickard et al., 2008 .”

We mindfully incorporated recommendations from (Pan & Rickard, 2015) into our own study designs including 1) utilizing 10s practice trials and 2) constraining our analysis of micro-offline gains to early learning trials (where performance monotonically increases and 95% of overall performance gains occur), which are prior to the emergence of the “scalloped” performance dynamics that are strongly linked to reactive inhibition effects.

However, there is no direct evidence in the literature that micro-offline gains really result from offline learning, i.e., an improvement in skill level.

We strongly disagree with the Reviewer’s assertion that “there is no direct evidence in the literature that micro-offline gains really result from offline learning, i.e., an improvement in skill level.” The initial (Bonstrup et al., 2019) report was followed up by a large online crowd-sourcing study (Bonstrup et al., 2020). This second (and much larger) study provided several additional important findings supporting our interpretation of micro-offline gains in cases where the important behavioral conditions clarified above were met (see Author response image 4 below for further details on these conditions).

Author response image 4.

This Figure shows that micro-offline gains o ser ed in learning and nonlearning contexts are attri uted to different underl ing causes. Micro-offline and online changes relative to overall trial-by-trial learning. This figure is based on data from (Bonstrup et al., 2019). During early learning, micro-offline gains (red bars) closely track trial-by-trial performance gains (green line with open circle markers), with minimal contribution from micro-online gains (blue bars). The stated conclusion in Bönstrup et al. (2019) is that micro-offline gains only during this Early Learning stage reflect rapid memory consolidation (see also (Bonstrup et al., 2020)). After early learning, about practice trial 11, skill plateaus. This plateau skill period is characterized by a striking emergence of coupled (and relatively stable) micro-online drops and micro-offline increases. Bönstrup et al. (2019) as well as others in the literature (Brooks et al., 2024; Gupta & Rickard, 2022; Florencia Jacobacci et al., 2020), argue that micro-offline gains during the plateau period likely reflect recovery from inhibitory performance factors such as reactive inhibition or fatigue, and thus must be excluded from analyses relating micro-offline gains to skill learning. The Non-repeating groups in Experiments 3 and 4 from Das et al. (2024) suffer from a lack of consideration of these known confounds (end of Fig legend).

Evidence documented in that paper (Bonstrup et al., 2020) showed that micro-offline gains during early skill learning were: 1) replicable and generalized to subjects learning the task in their daily living environment (n=389); 2) equivalent when significantly shortening practice period duration, thus confirming that they are not a result of recovery from performance fatigue (n=118); 3) reduced (along with learning rates) by retroactive interference applied immediately after each practice period relative to interference applied after passage of time (n=373), indicating stabilization of the motor memory at a microscale of several seconds consistent with rapid consolidation; and 4) not modified by random termination of the practice periods, ruling out a contribution of predictive motor slowing (N = 71) (Bonstrup et al., 2020). Altogether, our findings were strongly consistent with the interpretation that micro-offline gains reflect memory consolidation supporting early skill learning. This is precisely the portion of the learning curve (Pan & Rickard, 2015) refer to when they state “…rapid learning during that period masks any reactive inhibition effect”.

This interpretation is further supported by brain imaging evidence linking known memory-related networks and consolidation mechanisms to micro-offline gains. First, we reported that the density of fast hippocampo-neocortical skill memory replay events increases approximately three-fold during early learning inter-practice rest periods with the density explaining differences in the magnitude of micro-offline gains across subjects (Buch et al., 2021). Second, Jacobacci et al. (2020) independently reproduced our original behavioral findings and reported BOLD fMRI changes in the hippocampus and precuneus (regions also identified in our MEG study (Buch et al., 2021)) linked to micro-offline gains during early skill learning. These functional changes were coupled with rapid alterations in brain microstructure in the order of minutes, suggesting that the same network that operates during rest periods of early learning undergoes structural plasticity over several minutes following practice (Deleglise et al., 2023). Crucial to this point, Chen et al. (2024) and Sjøgård et al (2024) provided direct evidence from intracranial EEG in humans linking sharp-wave ripple density during rest periods (which are known markers for neural replay (Buzsaki, 2015)) in the human hippocampus (80-120 Hz) to micro-offline gains during early skill learning.

Thus, there is now substantial converging evidence in humans across different indirect noninvasive and direct invasive recording techniques linking hippocampal activity, neural replay dynamics and offline performance gains in skill learning.

On the contrary, recent evidence questions this interpretation (Gupta & Rickard, npj Sci Learn 2022; Gupta & Rickard, Sci Rep 2024; Das et al., bioRxiv 2024). Instead, there is evidence that micro-offline gains are transient performance benefits that emerge when participants train with breaks, compared to participants who train without breaks, however, these benefits vanish within seconds after training if both groups of participants perform under comparable conditions (Das et al., bioRxiv 2024).

The recent work of (Gupta & Rickard, 2022, 2024) does not present any data that directly opposes our finding that early skill learning (Bonstrup et al., 2019) is expressed as micro-offline gains during rest breaks. These studies are an extension of the Rickard et al (2008) paper that employed a massed (30s practice followed by 30s breaks) vs spaced (10s practice followed by 10s breaks) experimental design to assess if recovery from reactive inhibition effects could account for performance gains measured after several minutes or hours. Gupta & Rickard (2022) added two additional groups (30s practice/10s break and 10s practice/10s break as used in the work from our group). The primary aim of the study was to assess whether it was more likely that changes in performance when retested 5 minutes after skill training (consisting of 12 practice trials for the massed groups and 36 practice trials for the spaced groups) had ended reflected memory consolidation effects or recovery from reactive inhibition effects. The Gupta & Rickard (2024) follow-up paper employed a similar design with the primary difference being that participants performed a fixed number of sequences on each trial as opposed to trials lasting a fixed duration. This was done to facilitate the fitting of a quantitative statistical model to the data.

To reiterate, neither study included any analysis of micro-online or micro-offline gains and did not include any comparison focused on skill gains during early learning trials (only at retest 5 min later). Instead, Gupta & Rickard (2022), reported evidence for reactive inhibition effects for all groups over much longer training periods than early learning. In fact, we reported the same findings for trials following the early learning period in our original 2019 paper (Bonstrup et al., 2019) (Author response image 4). Please, note that we also reported that cumulative microoffline gains over early learning did not correlate with overnight offline consolidation measured 24 hours later (Bonstrup et al., 2019) (see the Results section and further elaboration in the Discussion). We interpreted these findings as indicative that the mechanisms underlying offline gains over the micro-scale of seconds during early skill learning versus over minutes or hours very likely differ.

In the recent preprint from (Das et al., 2024), the authors make the strong claim that “micro-offline gains during early learning do not reflect offline learning” which is not supported by their own data. The authors hypothesize that if “micro-offline gains represent offline learning, participants should reach higher skill levels when training with breaks, compared to training without breaks”. The study utilizes a spaced vs. massed practice groups between-subjects design inspired by the reactive inhibition work from Rickard and others to test this hypothesis.

Crucially, their design incorporates only a small fraction of the training used in other investigations to evaluate early skill learning (Bonstrup et al., 2020; Bonstrup et al., 2019; Brooks et al., 2024; Buch et al., 2021; Deleglise et al., 2023; F. Jacobacci et al., 2020; Mylonas et al., 2024). A direct comparison between the practice schedule designs for the spaced and massed groups in Das et al., and the training schedule all participants experienced in the original Bönstrup et al. (2019) paper highlights this issue as well as several others (Author response image 5):

Author response image 5.

This figure shows (A) Comparison of Das et al. Spaced & Massed group training session designs, and the training session design from the original (Bonstrup et al., 2019) paper. Similar to the approach taken by Das et al., all practice is visualized as 10-second practice trials with a variable number (either 0, 1 or 30) of 10-second-long inter-practice rest intervals to allow for direct comparisons between designs. The two key takeaways from this comparison are that (1) the intervention differences (i.e. – practice schedules) between the Massed and Spaced groups from the Das et al. report are extremely small (less than 12% of the overall session schedule) (gaps in the red shaded area) and (2) the overall amount of practice is much less than compared to the design from the original Bönstrup report (Bonstrup et al., 2019) (which has been utilized in several subsequent studies). (B) Group-level learning curve data from Bönstrup et al. (2019) (Bonstrup et al., 2019) is used to estimate the performance range accounted for by the equivalent periods covering Test 1, Training 1 and Test 2 from Das et al (2024). Note that the intervention in the Das et al. study is limited to a period covering less than 50% of the overall learning range (end of figure legend).

Participants in the original (Bonstrup et al., 2019) experienced 157.14% more practice time and 46.97% less inter-practice rest time than the Spaced group in the Das et al. study (Author response image 5). Thus, the overall amount of practice and rest differ substantially between studies, with much more limited training occurring for participants in Das et al.

In addition, the training interventions (i.e. – the practice schedule differences between the Spaced and Massed groups) were designed in a manner that minimized any chance of effectively testing their hypothesis. First, the interventions were applied over an extremely short period relative to the length of the total training session (5% and 12% of the total training session for Massed and Spaced groups, respectively; see gaps in the red shaded area in Author response image 5). Second, the intervention was applied during a period in which only half of the known total learning occurs. Specifically, we know from Bönstrup et al. (2019) that only 46.57% of the total performance gains occur in the practice interval covered by Das et al Training 1 intervention. Thus, early skill learning as evaluated by multiple groups (Bonstrup et al., 2020; Bonstrup et al., 2019; Brooks et al., 2024; Buch et al., 2021; Deleglise et al., 2023; F. Jacobacci et al., 2020; Mylonas et al., 2024), is in the Das et al experiment amputated to about half.

Furthermore, a substantial amount of learning takes place during Das et al’s Test 1 and Test 2 periods (32.49% of total gains combined). The fact that substantial learning is known to occur over both the Test 1 (18.06%) and Test 2 (14.43%) intervals presents a fundamental problem described by Pan and Rickard (Pan & Rickard, 2015). They reported that averaging over intervals where substantial performance gains occur (i.e. – performance is not stable) inject crucial artefacts into analyses of skill learning:

“A large amount of averaging has the advantage of yielding more precise estimates of each subject’s pretest and posttest scores and hence more statistical power to detect a performance gain. However, calculation of gain scores using that strategy runs the risk that learning that occurs during the pretest and (or posttest periods (i.e., online learning is incorporated into the gain score (Rickard et al., 2008; Robertson et al., 2004 .”

The above statement indicates that the Test 1 and Test 2 performance scores from Das et al. (2024) are substantially contaminated by the learning rate within these intervals. This is particularly problematic if the intervention design results in different Test 2 learning rates between the two groups. This in fact, is apparent in their data (Figure 1C,E of the Das et al., 2024 preprint) as the Test 2 learning rate for the Spaced group is negative (indicating a unique interference effect observable only for this group). Specifically, the Massed group continues to show an increase in performance during Test 2 and 4 relative to the last 10 seconds of practice during Training 1 and 2, respectively, while the Spaced group displays a marked decrease. This post-training performance decrease for the Spaced group is in stark contrast to the monotonic performance increases observed for both groups at all other time-points. One possible cause could be related to the structure of the Test intervals, which include 20 seconds of uninterrupted practice. For the Spaced group, this effectively is a switch to a Massed practice environment (i.e., two 10-secondlong practice trials merged into one long trial), which interferes with greater Training 1 interval gains observed for the Space group. Interestingly, when statistical comparisons between the groups are made at the time-points when the intervention is present (Figure 1E) then the stated hypothesis, “If micro-offline gains represent offline learning, participants should reach higher skill levels when training with breaks, compared to training without breaks”, is confirmed.

In summary, the experimental design and analyses used by Das et al does not contradict the view that early skill learning is expressed as micro-offline gains during rest breaks. The data presented by Gupta and Rickard (2022, 2024) and Das et al. (2024) is in many ways more confirmatory of the constraints employed by our group and others with respect to experimental design, analysis and interpretation of study findings, rather than contradictory. Still, it does highlight a limitation of the current micro-online/offline framework, which was originally only intended to be applied to early skill learning over spaced practice schedules when reactive inhibition effects are minimized (Bonstrup et al., 2019; Pan & Rickard, 2015). Extrapolation of this current framework to postplateau performance periods, longer timespans, or non-learning situations (e.g. – the Nonrepeating groups from Das et al. (2024)), when reactive inhibition plays a more substantive role, is not warranted. Ultimately, it will be important to develop new paradigms allowing one to independently estimate the different coincident or antagonistic features (e.g. - memory consolidation, planning, working memory and reactive inhibition) contributing to micro-online and micro-offline gains during and after early skill learning within a unifying framework.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) I found Figure 2B too small to be useful, as the actual elements of the cells are very hard to read.

We have removed the grid colormap panel (top-right) from Figure 2B. All of this colormap data is actually a subset of data presented in Figure 2 – figure supplement 1, so can still be found there.

Reviewer #2 (Recommendations for the authors):

(1) Related to the first point in my concerns, I would suggest the authors compare decoding accuracy between correct presses followed by correct vs. incorrect presses. This would clarify if the decoder is actually taking the MEG signal for subsequent press into account. I would also suggest the authors use pre-movement MEG features and post-movement features with shorter windows and compare each result with the results for the original post-movement MEG feature with a longer window.

The present study does not contain enough errors to perform the analysis proposed by the Reviewer. As noted above, we did re-examine our data and now report a new control regression analysis, all of which indicate that the proximity between keypresses does not explain contextualization effects.

(2) I was several times confused by the author's use of "neural representation of an action" or "sequence action representations" in understanding whether these terms refer to representation on the level of whole-brain, region (as defined by the specific parcellation used), or voxels. In fact, what is submitted to the decoder is some complicated whole-brain MEG feature (i.e., the "neural representation"), which is a hybrid of voxel and parcel features that is further dimension-reduced and not immediately interpretable. Clarifying this point early in the text and possibly using some more sensible terms, such as adding "brain-wise" before the "sequence action representation", would be the most helpful for the readers.

We now clarified this terminology in the revised manuscript.

(3) Although comparing many different ways in feature selection/reduction, time window selection, and decoder types is undoubtedly a meticulous work, the current version of the manuscript seems still lacking some explanation about the details of these methodological choices, like which decoding method was actually used to report the accuracy, whether or not different decoding methods were chosen for individual participants' data, how training data was selected (is it all of the correct presses in Day 1 data?), whether the frequency power or signal amplitude was used, and so on. I would highly appreciate these additional details in the Methods section.

The reported accuracies were based on linear discriminant analysis classifier. A comparison of different decoders (Figure 3 – figure supplement 4) shows LDA was the optimal choice.

Whether or not different decoding methods were chosen for individual participants' data

We selected the same decoder (LDA) performance to report the final accuracy.

How training data was selected (is it all of the correct presses in Day 1 data?),

Decoder training was conducted as a randomized split of the data (all correct keypresses of Day 1) into training (90%) and test (10%) samples for 8 iterations.

Whether the frequency power or signal amplitude was used

Signal amplitude was used for feature calculation.

(4) In terms of the Methods, please consider adding some references about the 'F1 score', the 'feature importance score,' and the 'MRMR-based feature ranking,' as the main readers of the current paper would not be from the machine learning community. Also, why did the LDA dimensionality reduction reduce accuracy specifically for the voxel feature?

We have now added the following statements to the Methods section that provide more detailed descriptions and references for these metrics:

“The F1 score, defined as the harmonic mean of the precision (percentage of true predictions that are actually true positive) and recall (percentage of true positives that were correctly predicted as true) scores, was used as a comprehensive metric for all one-versus-all keypress state decoders to assess class-wise performance that accounts for both false-positive and false-negative prediction tendencies [REF]. A weighted mean F1 score was then computed across all classes to assess the overall prediction performance of the multi-class model.”

and

“Feature Importance Scores

The relative contribution of source-space voxels and parcels to decoding performance (i.e. – feature importance score) was calculated using minimum redundant maximum relevance (MRMR) and highlighted in topography plots. MRMR, an approach that combines both relevance and redundancy metrics, ranked individual features based upon their significance to the target variable (i.e. – keypress state identity) prediction accuracy and their non-redundancy with other features.”

As stated in the Reviewer responses above, the dimensionality of the voxel-space feature set is very high (i.e. – 15684). LDA attempts to map the input features onto a much smaller dimensional space (number of classes-1; e.g. – 3 dimensions for 4-class keypress decoding). It is likely that the reduction in accuracy observed only for the voxel-space feature was due to the loss of relevant information during the mapping process that resulted in reduced accuracy. This reduction in accuracy for voxel-space decoding was specific to LDA. Figure 3—figure supplement 3 shows that voxel-space decoder performance actually improved when utilizing alternative dimensionality reduction techniques.

(5) Paragraph 9, lines #139-142: "Notably, decoding associated with index finger keypresses (executed at two different ordinal positions in the sequence) exhibited the highest number of misclassifications of all digits (N = 141 or 47.5% of all decoding errors; Figure 3C), raising the hypothesis that the same action could be differentially represented when executed at different learning state or sequence context locations."

This does not seem to be a fair comparison, as the index finger appears twice as many as the other fingers do in the sequence. To claim this, proper statistical analysis needs to be done taking this difference into account.

We thank the Reviewer for bringing this issue to our attention. We have now corrected this comparison to evaluate relative false negative and false positive rates between individual keypress state decoders, and have revised this statement in the manuscript as follows:

“Notably, decoding of index finger keypresses (executed at two different ordinal positions in the sequence) exhibited the highest false negative (0.116 per keypress) and false positive (0.043 per keypress) misclassification rates compared with all other digits (false negative rate range = [0.067 0.114]; false positive rate range = [0.020 0.037]; Figure 3C), raising the hypothesis that the same action could be differentially represented when executed within different contexts (i.e. - different learning states or sequence locations).”

(6) Finally, the authors could consider acknowledging in the Discussion that the contribution of micro-offline learning to genuine skill learning is still under debate (e.g., Gupta and Rickard, 2023; 2024; Das et al., bioRxiv, 2024).

We have added a paragraph in the Discussion that addresses this point.

Reviewer #3 (Recommendations for the authors):

In addition to the additional analyses suggested in the public review, I have the following suggestions/questions:

(1) Given that the authors introduce a new decoding approach, it would be very helpful for readers to see a distribution of window sizes and window onsets eventually used across individuals, at least for the optimized decoder.

We have now included a new supplemental figure (Figure 4 – figure Supplement 2) that provides this information.

(2) Please explain in detail how you arrived at the (interpolated?) group-level plot shown in Figure 1B, starting from the discrete single-trial keypress transition times. Also, please specify what the shading shows.

Instantaneous correct sequence speed (skill measure) was quantified as the inverse of time (in seconds) required to complete a single iteration of a correctly generated full 5-item sequence. Individual keypress responses were labeled as members of correct sequences if they occurred within a 5-item response pattern matching any possible circular shifts of the 5-item sequence displayed on the monitor (41324). This approach allowed us to quantify a measure of skill within each practice trial at the resolution of individual keypresses. The dark line indicates the group mean performance dynamics for each trial. The shaded region indicates the 95% confidence limit of the mean (see Methods).

(3) Similarly, please explain how you arrived at the group-level plot shown in Figure 1C. What are the different colored lines (rows) within each trial? How exactly did the authors reach the conclusion that KTT variability stabilizes by trial 6?

Figure 1C provides additional information to the correct sequence speed measure above, as it also tracks individual transition speed composition over learning. Figure 1C, thus, represents both changes in overall correct sequence speed dynamics (indicated by the overall narrowing of the horizontal speed lines moving from top to bottom) and the underlying composition of the individual transition patterns within and across trials. The coloring of the lines is a shading convention used to discriminate between different keypress transitions. These curves were sampled with 1ms resolution, as in Figure 1B. Addressing the underlying keypress transition patterns requires within-subject normalization before averaging across subjects. The distribution of KTTs was normalized to the median correct sequence time for each participant and centered on the mid-point for each full sequence iteration during early learning.

(4) Maybe I missed it, but it was not clear to me which of the tested classifiers was eventually used. Or was that individualized as well? More generally, a comparison of the different classifiers would be helpful, similar to the comparison of dimension reduction techniques.

We have now included a new supplemental figure that provides this information.

(5) Please add df and effect sizes to all statistics.

Done.

(6) Please explain in more detail your power calculation.

The study was powered to determine the minimum sample size needed to detect a significant change in skill performance following training using a one-sample t-test (two-sided; alpha = 0.05; 95% statistical power; Cohen’s D effect size = 0.8115 calculated from previously acquired data in our lab). The calculated minimum sample size was 22. The included study sample size (n = 27) exceeded this minimum.

This information is now included in the revised manuscript.

(7) The cut-off for the high-pass filter is unusually high and seems risky in terms of potential signal distortions (de Cheveigne, Neuron 2019). Why did the authors choose such a high cut-off?

The 1Hz high-pass cut-off frequency for the 1-150Hz band-pass filter applied to the continuous raw MEG data during preprocessing has been used in multiple previous MEG publications (Barratt et al., 2018; Brookes et al., 2012; Higgins et al., 2021; Seedat et al., 2020; Vidaurre et al., 2018).

(8) "Furthermore, the magnitude of offline contextualization predicted skill gains while online contextualization did not", lines 336/337 - where is that analysis?

Additional details pertaining to this analysis are now provided in the Results section (Figure 5 – figure supplement 4).

(9) How were feature importance scores computed?

We have now added a new subheading in the Methods section with a more detailed description of how feature importance scores were computed.

(10)  Please add x and y ticks plus tick labels to Figure 5 - Figure Supplement 3, panel A

Done

(11) Line 369, what does "comparable" mean in this context?

The sentence in the “Study Participants” part of the Methods section referred to here has now been revised for clarity.

(12) In lines 496/497, please specify what t=0 means (KeyDown event, I guess?).

Yes, the KeyDown event occurs at t = 0. This has now been clarified in the revised manuscript.

(13) Please specify consistent boundaries between alpha- and beta-bands (they are currently not consistent in the Results vs. Methods (14/15 Hz or 15/16 Hz)).

We thank the Reviewer for alerting us to this discrepancy caused by a typographic error in the Methods. We have now corrected this so that the alpha (8-14 Hz) and beta-band (15-24 Hz) frequency limits are described consistently throughout the revised manuscript.

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Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this study, Basha and colleagues aim to test whether the thalamic nucleus reuniens can facilitate the hippocampus/prefrontal cortex coupling during sleep. Considering the importance of sleep in memory consolidation, this study is important to understand the functional interaction between these three majorly involved regions. This work suggests that the thalamic nucleus reuniens has a functional role in synchronizing the hippocampus and prefrontal cortex.

Strengths:

The authors performed recordings in naturally sleeping cats, and analysed the correlation between the main slow wave sleep oscillatory hallmarks: slow waves, spindles, and hippocampal ripples, and with reuniens' neurons firing. They also associated intracellular recordings to assess the reuniens-prefrontal connectivity, and computational models of large networks in which they determined that the coupling of oscillations is modulated by the strength of hippocampal-thalamic connections.

Thank you for your positive evaluation.

Weaknesses:

The authors' main claim is made on slow waves and spindle coupling, which are recorded both in the prefrontal cortex and surprisingly in reuniens. Known to be generated in the cortex by cortico-thalamic mechanisms, the slow waves and spindles recorded in reuniens show no evidence of local generation in the reuniens, which is not anatomically equipped to generate such activities. Until shown differently, these oscillations recorded in reuniens are most likely volume-conducted from nearby cortices. Therefore, such a caveat is a major obstacle to analysing their correlation (in time or frequency domains) with oscillations in other regions.

(1) We fully agree with the reviewer that reuniens likely does not generate neither slow waves nor spindles. We do not make such claim, which we clearly stated in the discussion (lines 319-324). We propose that Reuniens neurons mediate different forms of activity. In the model, we introduced MD nucleus only because without MD we were unable to generate spindles. While the slow waves and spindles are generated in other thalamocortical regions, the REU neurons show these rhythms due to long-range projections from these regions to REU as has been shown in the model.

(2) Definitely, we cannot exclude some influence of volume conductance on obtained LFP recordings in REU nucleus. However, we show modulation of spiking activity within REU by spindles. Spike modulation cannot be explained by volume conductance but can be explained by either synaptic drive (likely the case here) or some intrinsic neuronal processes (like T-current).

(3) In our REU recordings for spike identification we used tetrode recordings. If slow waves and spindles are volume conducted, then slow waves and spindles recorded with tetrodes should have identical shape. Following reviewer comment, we took these recordings and subtracted one channel from another. The difference in signal during slow waves is in the order 0.1 mV. Considering that the distance between electrodes is in the order of 20 um, such a difference in voltage is major and can only be explained by local extracellular currents, likely due to synaptic activities originating in afferent structures.

Finally, the choice of the animal model (cats) is the best suited one, as too few data, particularly anatomical ones regarding reuniens connectivity, are available to support functional results.

(1) Thalamus of majority of mammals (definitely primates and carnivores, including cats) contain local circuit interneurons (about 30 % of all neurons). A vast majority of studies in rodents (except LGN nucleus) report either absence or extremally low (i.e. Jager P, Moore G, Calpin P, et al. Dual midbrain and forebrain origins of thalamic inhibitory interneurons. eLife. 2021; 10: e59272.) number of thalamic interneurons. Therefore, studies on other species than rodents are necessary, and bring new information, which is impossible to obtain in rodents.

(2) Cats’ brain is much larger than the brain of mice or rats, therefore, the effects of volume conductance from cortex to REU are much smaller, if not negligible. The distance between REU and closest cortical structure (ectosylvian gyrus) in cats is about 15 mm.

(3) Indeed, there is much less anatomical data on cats as opposed to rodents. This is why, we performed experiments shown in the figure 1. This figure contains functional anatomy data. Antidromic responses show that recorded structure projects to stimulated structure. Orthodromic responses show that stimulated structure projects to recorded structure.

Reviewer #2 (Public Review):

Summary:

The interplay between the medial prefrontal cortex and ventral hippocampal system is critical for many cognitive processes, including memory and its consolidation over time. A prominent idea in recent research is that this relationship is mediated at least in part by the midline nucleus reuniens with respect to consolidation in particular. Whereas the bulk of evidence has focused on neuroanatomy and the effects of temproary or permanent lesions of the nucleus reuniens, the current work examined the electrophysiology of these three structures and how they inter-relate, especially during sleep, which is anticipated to be critical for consolidation. They provide evidence from intercellular recordings of the bi-directional functional connectivity among these structures. There is an emphasis on the interactions between these regions during sleep, especially slow-wave sleep. They provide evidence, in cats, that cortical slow waves precede reuniens slow waves and hippocampal sharp-wave ripples, which may reflect prefrontal control of the timing of thalamic and hippocampal events, They also find evidence that hippocampal sharp wave ripples trigger thalamic firing and precede the onset of reuniens and medial prefrontal cortex spindles. The authors suggest that the effectiveness of bidirectional connections between the reuniens and the (ventral) CA1 is particularly strong during non-rapid eye movement sleep in the cat. This is a very interesting, complex study on a highly topical subject.

Strengths:

An excellent array of different electrophysiological techniques and analyses are conducted. The temporal relationships described are novel findings that suggest mechanisms behind the interactions between the key regions of interest. These may be of value for future experimental studies to test more directly their association with memory consolidation.

We thank this reviewer for very positive evaluation of our study.

Weaknesses:

Given the complexity and number of findings provided, clearer explanation(s) and organisation that directed the specific value and importance of different findings would improve the paper. Most readers may then find it easier to follow the specific relevance of key approaches and findings and their emphasis. For example, the fact that bidirectional connections exist in the model system is not new per se. How and why the specific findings add to existing literature would have more impact if this information was addressed more directly in the written text and in the figure legends.

Thank you for this comment. In the revised version, we will do our best to simplify presentation and more clearly explain our findings.

Reviewing Editor (Recommendations for Authors):

Please discuss the ability of reuniens to generate spindles?

We briefly discussed this in previous version. We now extended the discussion (p. 18).

For population data, how many cats were used in acute and chronic experiments, where does the population data originate in Fig. 2? How repeatable were the findings across animals? Was histology verified in each animal?

As previously stated in the beginning of method section we totally used 20 cats: 16 anesthetized (or acute) and 4 non-anesthetized (or chronic). We added number of cats in appropriate places in the result section. Population data in figure 2 comes from 48, 49 or 52 recording sessions (depending on the type of analysis, and indicated in the figure legend) from 4 chronic cats; we clarified this information in the legend. Results were highly repeatable across animals. Histology was verified in all chronic and acute animals, we added a sentence in the method section.

Explanation of figures is very poor, values in figures should be reported in results so they can be compared in the context of the description.

In this revised version, we report most numbers present in figures and their legend to the main text (result section).

The depth of the recording tungsten electrodes are meaningless without the AP and ML coordinates given how heterogenous mPFC is. What is the ventromedial wall of the mPFC in the cat?

We added the ML and AP coordinates in the method section. We corrected ventromedial wall for ventroposterior part of the mPFC.

What are the two vertical lines in 1F?

This was an error while preparing the figure. The panel was corrected.

Line 90 mean +-SD of what? There are no numbers.

Thanks, we now indicate the values.

Panel 2L does not show increased spindling in reuniens prior to PFC as indicated in the results, please explain. It does show SWR in the hippocampus prior to spindles, what is the meaning of such a time relationship?

Panel 2L did show an increased spindling reuniens prior to mPFC, but indeed at the time scale shown, it was not very clear. In this revised manuscript, we added an inset zooming around time zero to make this point clearer.

Panel 2L indeed show an increase in SWR prior to the increase in spindle in both Reuniens and mPFC.

As stated in the discussion, ‘We found that hippocampal SWRs trigger thalamic firing and precede the onset of reuniens and mPFC spindles, which points to SWRs as one of candidate events for spindle initiation.’

It is unclear what the slow waves of PFC mean, these represent filtered PFC lfp, but is this a particular oscillation? They continue to occur during the spindle, while the slow waves supposedly trigger the spindle. Please explain and clarify.

We recently published a review article involving several scientists studying both human and animal sleep that has inserted Box. 1 (Timofeev I, Schoch S, LeBourgeois M, Huber R, Riedner B, Kurth S. Spatio-temporal properties of sleep slow waves and implications for development. Current Opinion in Physiology. 2020; 15: 172–182). In this box among other terms, we provide current definition of slow waves vs slow oscillation. Briefly, if slow waves are repeated with a given rhythm, they typically form slow oscillation. However, if they occur in isolation or are not rhythmic, they remain slow waves, but cannot be called slow oscillation.

Regarding relation of spindles and slow oscillation. We are currently systematically analyzing data on spindles and slow waves obtained from head-restrained and freely behaving cats. One of the main findings is that a majority of ‘cortical’ spindles are local. Local to the extent that spindles can occur in alternation in two neighboring cortical cells. Largely, LFP sleep spindles occur more or less synchronously within suprasylvian gyrus of cats where indeed a large majority of them was triggered by slow waves. The synchrony between LFP spindles in suprasylvian vs other other cortical areas is much less clear. So, it is not surprizing that spindles in one bran region can occur when there is a slow wave present in some other brain region. Something of a kind was also shown in human (Mölle M, Bergmann TO, Marshall L, Born J. Fast and slow spindles during the sleep slow oscillation: disparate coalescence and engagement in memory processing. Sleep. 2011; 34 (10): 1411-1421).

In this regard, we are not ready to include modifications in the manuscript.

Line 134, where is spindle amplitude shown? Plots report power within the spindle frequency band, which obviously captures more than just spindles.

No, plots of figure 3 B, C show the phase-amplitude coupling (PAC) strength. These were calculated with detected spindles, therefore, while we cannot exclude some false spindle detections, we are confident that the false spindle detections are at a negligible level. We modified text and instead of spindle amplitude, we describe SW-spindle amplitude coupling. This reflects our analysis with exactitude.

The discussion must include the medio dorsal nucleus which is the largest thalamic input to the prefrontal cortex and also receives input from the hippocampus. In particular, the case must be made for why reuniens would play a more important or different role than MD? (For example: Occurrence of Hippocampal Ripples is Associated with Activity Suppression in the Mediodorsal Thalamic Nucleus - PMC (nih.gov)).

We cited the suggested study. We cannot say whether reuniens plays a more or less important role. What is clear is that hippocampal ripples at the onset of spindles trigger increased firing in both MD and reuniens. Our extracellular recordings (Fig. 4, K) suggest that the increased firing is associated with spike-bursts. We also have a parallel unpublished study done on anesthetized mice showing SWR triggered inhibitory potentials in both reuniens and MD that reverses around -65mV - -70 mV. Because the majority of SWR occurred at the onset of cortical up state, a relative role of cortico-thalamic vs hippocampo-thalamic drive is not easy to separate. We hope, we will convincingly do this in our forthcoming study, with the limitation that it was done on anesthetized mice.

Reviewer #1 (Recommendations For The Authors):

I strongly encourage the authors to perform current source density analyses on the LFP signals recorded in the nucleus reuniens to make sure that the observed oscillations are indeed locally generated. So far, the anatomical organisation in reuniens cannot support the local generation of oscillations, such as spindles and slow wave. At least in rodents (the cat reuniens does not seem too different, until shown differently), there were no oscillators found in reuniens, and at least not arranged like in cortical areas, allowing the summation in time, and particularly space, of rhythmic input currents. Bipolar recordings with pairs of twisted electrodes might also be useful to assess the local existence of spindles and slow waves.

Current source density calculation is possible when one knows the exact distance between recording sites. As we used tetrodes made with 4 twisted platinum-iridium wires, we know more or less the range of distance between recording sites, but not the exact distance between any given pair of electrodes.

Then, the physical distance between the reuniens and any cortical structure is about 8-9 mm. Therefore, with such distances, volume conductance is expected to be negligible. If slow waves and spindles are volume conducted, then slow waves and spindles recorded with tetrodes should have identical shape. Following reviewer comment, we took these recordings and subtracted one channel from another. The difference in signal during slow waves is in the order 0.1 mV. Considering that the distance between electrodes is in the order of 20 um, such a difference in voltage is major and can only be explained by local extracellular currents, likely due to synaptic activities originating in afferent structures.

Below, we plotted the voltage of one channel of the tetrode versus another channel of the same tetrode. If the signal was simply volume conducted, one would expect to see the vast majority of points on the x=y line (red).

Author response image 1.

Below is a segment of mPFC LFP recording (upper black trace), mPFC LFP filtered for spindle frequency (7-15 Hz) and the spindle detected (black lines above the filtered trace. Then two LFP traces from a tetrode in the Reuniens (orange and light blue) are overlayed. The second trace (Blue) from bottom represents the substraction of Reuniens 1 minus Reuniens 2 channel, and just below (lower Blue trace) is this susbtraction trace filtered for spindle frequency (7-15 Hz) showing clear voltage difference in the spindle range between the two electrodes. Note also that around time 179-179.5 s, there is clear spindle oscillation in the mPFC recording which is not present in the Reuniens recordings.

Author response image 2.

Therefore, we are convinced that in our recordings, volume conductance did not play any significant role.

Another concern regarding delays between events, like slow waves, measured between two regions (as exemplified by Figure 3). It appears that the delays were calculated from the filtered signal. Figure 3G shows a delay between the peak of the mPFC slow wave between the raw and the filtered signal, which might be artifactual of the processing. It is though not (or less) visible for the reuniens recording. Such mismatch might explain the observed differences in delays.

Thanks for this comment. We recomputed the analysis using the original signal (smoothed) and obtained very similar results. Panels H and I of figure 3 were updated using the new analysis performed on original signal.

The overall analyses of LFP-triggered reuniens MUA activity lack of statistics (at least z-scored firing to normalise the firings).

Fig. 2 H and I are representative examples for histograms; statistical data are shown in circular plots as explained in the legend. Fig. 2 L, shows populational data and we provide now standard error. Fig. 4 C and D show individual example. Fig. 4 E shows histograms of activity of all identified putative single units. Units that show significant modulation are displayed above white line. Fig. 4 F shows populational data for significantly modified units.  

A last point of detail in the model, which surprisingly shows reuniens to excitatory hippocampal cells' connectivity. Recent literature reports that reuniens only connect hippocampal interneurons, and not principal cells (at least in rodents, I could not find any report in cats). I wonder how changing this parameter would affect the results of the computational investigation, particularly the results shown in Figure 6.

There are several studies in the literature showing a direct excitation from the Reuniens to pyramidal cells in the CA1, here are three of them:

Goswamee, P., et al. (2021). "Nucleus Reuniens Afferents in Hippocampus Modulate CA1 Network Function via Monosynaptic Excitation and Polysynaptic Inhibition." Frontiers in Cellular Neuroscience 15.

Dolleman-Van der Weel MJ, Lopes da Silva FH, Witter MP (1997) Nucleus Reuniens Thalami Modulates Activity in Hippocampal Field CA1 through Excitatory and Inhibitory Mechanisms. The Journal of Neuroscience 17:5640.

Dolleman-van der Weel MJ, Lopes da Silva FH, Witter MP (2017) Interaction of nucleus reuniens and entorhinal cortex projections in hippocampal field CA1 of the rat. Brain Structure and Function 222:2421-2438.

Because this is not a review paper, we opted to not cite all the papers describing connectivity between mPFC, hippocampus and thalamus.

Reviewer #2 (Recommendations For The Authors):

I respectively suggest that the earlier (public) comments listed above should be addressed. In addition, it would be useful to make it clearer when non-rapid eye movement sleep was being addressed and when rapid eye movement was being addressed. Is it of value to use a single term instead of adding "slow wave sleep" or else clarify when either term is used? The addition of more subheadings might help. Moreover, the relative contribution/value of evidence from these two sleep states was not addressed or was not very clear.

We tried to make it clearer when NREM and when REM was analysed.

We replaced slow-wave sleep with NREM sleep in the figure 5 title.

We added several subheadings in the discussion.

Relative contribution of NREM vs REM sleep was not addressed? Sorry but we do not clearly understand your question. Figs. 2 and 3 deal mainly with NREM sleep (Fig 2.B has an example of REM sleep). Fig. 4 essentially describes results obtained during REM sleep.

I was not sure if the Abstract summarised the key take-home messages from the large amount of evidence provided. Some choices are needed, of course, but "evidence of bidirectional connectivity" struck me as less novel than other evidence provided. Given the huge amount of findings provided, which is commendable, it is still useful to present it perhaps in a more digestible fashion. For example, the headings or the first sentence(s) below headings could indicate the aim or the outcome of the specific method/analysis/findings.

We rewrote abstract and we also added some conclusion to highlight major findings and their meaning.

It is more common to use NRe or Re, rather than REU.

We avoided using RE as, for decades, we used RE to abbreviate the thalamic reticular nucleus in several publications. In this revised version, we spell at full - Reuniens.

Line 49 mentions "short-term" memory. Please specify this more clearly as it is otherwise ambiguous. Also, line 303.

We rephrased the sentence: In particular, the hierarchical coupling of slow waves, spindles and SWRs is thought to play a key role in memory consolidation.

Line 303 was likely about the ventromedial wall: we corrected that sentence.

Line 62: the word, "required" (for memory function) is too strong because there is evidence that it is not always required.

We modified the sentence for plays a major role.

The focus within the medial prefrontal cortex could be specified more clearly / earlier.

The mPFC is mentioned in the second sentence of the abstract and in the first sentence of the introduction.

Line 134: The heading states "determine" and then mentions modulation. These terms may not be interchangeable or they need clarification.

We changed it to slow wave-spindle amplitude coupling. This represents exactly our analysis.

Line 204: Does "cortical network" mean prefrontal cortex network"?

Yes, as described in lines 192-193, the two cortical networks (N1 and N2) of the model represent the mPFC layer 5 and 6 respectively.

Lines 283 to 289: These were not very clear to me.

These lines described the potential mechanisms for the responses to hippocampal and reuniens stimulation recorded intracellularly (results in figure 1). We modified this paragraph for clarity.

Line 296: Specify the "claim".

We modified the sentence for “[…] provides supporting evidence for this claim that nucleus Reuniens might synchronize the activity of ventral hippocampus and mPFC.”

The discussion naturally focuses on the thalamic nucleus reuniens, but also occasionally mentions the thalamic mediodorsal nucleus. The distinction, assuming this is highly relevant, could be expressed more clearly (direct comparison with their previous papers).

We never published a study on the mediodorsal nucleus. We do have some unpublished results from recordings in the MD nucleus and they reveal the presence of an inhibitory component at the beginning of cortical active states, therefore behaving in a similar way to first order nuclei. It is then possible that spindles recorded in the reuniens are actually generated in the MD nucleus and then transmitted to Reuniens through the thalamic reticular nucleus, as both MD and reuniens are connected to the rostral thalamic reticular nucleus. We added some discussion about this.

Figure 1B: Do the authors have any additional evidence of the placements in the reuniens, because the photo provided suggests a large area beyond the reuniens boundary. Also, please confirm is the CEM between Rh and Re in the cat (I think the Rh and Re are adjacent in the rat).

Figure 1B is from an electrolytic lesion, which is necessarily bigger than the tip of the electrode. Therefore the center of the electrolytic lesion indicates where the electrode tip was located which is well within the reuniens nucleus.

Also, yes CE (Nucleus centralis thalami, pars medialis) is located between the reuniens and rhomboid in cats. This can be found in two cat atlas:  

Reinoso-Suárez, F. (1961). Topographischer Hirnatlas der Katze für experimental-physiologische Untersuchungen (Merck).

Berman AL, Jones EG (1982) The Thalamus and Basal Telencephalon of the Cat: A Cytoarchitectonic Atlas with Stereotaxic Coordinates: University of Wisconsin Press.

The first mention of hippocampus in the figure legends should remind the reader by stating "ventral hippocampus".

In this revised version, we added “ventral” in several instances both in the main text and in figure legend.

Figure 2: It seems unusual to mention "unusually short NREM". Presumably, things are the same otherwise - if so, perhaps mention that, especially if some of the effects reflect an "unusual" episode.

We display this particular segment because we want to show continuous recording in which still individual elements characterizing specific states are still visible.

Some effects look like they are strong and others perhaps weaker. If so, how do these impact the final conclusions?

Sorry, we did not understand clearly what is meant here by the reviewer. In general, if any effect has statistically significant difference (old fashion 0.05) we consider it as significant. Any other cases are described on individual basis.

Perhaps "MAD" should be in full on the first occasion, if not already.

It was spelled out at line 659, but we now spell it out also in the results section and in figure 2 legend.

Methods: the key question is the use of rodent recordings to classify cat recordings. It would be good to have a reference indicating that this can be directly used for cats, which may have different sleep cycles and patterns compared to rats.

We did not use rodent recordings to classify cat recordings, however we did used a state detection script that was developed with rodent recordings. As mentioned in the method section, we adapted the script to cat mPFC recordings and then manual corrections were made to correctly detect REM episodes. Respectfully, our lab investigates sleep-wake in non-anesthetized animals for a few decades; we developed state detection algorithm in mice, cats, marmosets when needed (to analyse months of recordings), and we have an extensive expertise in identifying states of vigilance from electrophysiological recordings.

Author response:

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

Public Reviews:

Summary:

The authors examine the eigenvalue spectrum of the covariance matrix of neural recordings in the whole-brain larval zebrafish during hunting and spontaneous behavior. They find that the spectrum is approximately power law, and, more importantly, exhibits scale-invariance under random subsampling of neurons. This property is not exhibited by conventional models of covariance spectra, motivating the introduction of the Euclidean random matrix model. The authors show that this tractable model captures the scale invariance they observe. They also examine the effects of subsampling based on anatomical location or functional relationships. Finally, they briefly discuss the benefit of neural codes which can be subsampled without significant loss of information.

Strengths:

With large-scale neural recordings becoming increasingly common, neuroscientists are faced with the question: how should we analyze them? To address that question, this paper proposes the Euclidean random matrix model, which embeds neurons randomly in an abstract feature space. This model is analytically tractable and matches two nontrivial features of the covariance matrix: approximate power law scaling, and invariance under subsampling. It thus introduces an important conceptual and technical advance for understanding large-scale simultaneously recorded neural activity.

Weaknesses:

The downside of using summary statistics is that they can be hard to interpret. Often the finding of scale invariance, and approximate power law behavior, points to something interesting. But here caution is in order: for instance, most critical phenomena in neural activity have been explained by relatively simple models that have very little to do with computation (Aitchison et al., PLoS CB 12:e1005110, 2016; Morrell et al., eLife 12, RP89337, 2024). Whether the same holds for the properties found here remains an open question.

We are grateful for the thorough and constructive feedback provided on our manuscript. We have addressed each point raised by you.

Regarding the main concern about power law behavior and scale invariance, we would like to clarify that our study does not aim to establish criticality. Instead, we focus on describing and understanding a specific scale-invariant property in terms of collapsed eigenspectra in neural activity. We tested Morrell et al.’s latent-variable model (eLife 12, RP89337, 2024, [1]), where a slowly varying latent factor drives population activity. Although it produces a seemingly power-law-like spectrum, random sampling does not replicate the strict spectral collapse observed in our data (second row in Fig. S23). This highlights that simply adding latent factors does not fully recapitulate the scale invariance we measure, suggesting richer or more intricate processes may be involved in real neural recordings.

Specifically, we have incorporated five key revisions.

• As mentioned, we evaluated the latent variable model proposed by Morrell et al., and found that they fail to reproduce the scale-invariant eigenspectra observed in our data; these results are now presented in the Discussion section and supported by a new Supplementary Figure (Fig. S23).

• We included a comparison with the findings of Manley et al. (2024 [2]) regarding the issue of saturating dimension in the Discussion section, highlighting the methodological differences and their implications.

• We added a new mathematical derivation in the Methods section, elucidating the bounded dimensionality using the spectral properties of our model. • We have added a sentence in the Discussion section to further emphasize the robustness of our findings by demonstrating their consistency across diverse datasets and experimental techniques.

• We have incorporated a brief discussion on the implications for neural coding (lines 330-332). In particular, Fisher information can become unbounded when the slope of the power-law rank plot is less than one, as highlighted in the recent work by Moosavi et al. (bioRxiv 2024.08.23.608710, Aug, 2024 [3]).

We believe these revisions address the concerns raised during the review process and collectively strengthen our manuscript to provides a more comprehensive and robust understanding of the geometry and dimensionality of brain-wide activity. We appreciate your consideration of our revised manuscript and look forward to your feedback.

Recommendations for the authors:

In particular, in our experience replies to the reviewers are getting longer than the paper, and we (and I’m sure you!) want to avoid that. Maybe just reply explicitly to the ones you disagree with? We’re pretty flexible on our end.

(1) The main weakness, from our point of view, is whether the finding of scale invariance means something interesting, or should be expected from a null model. We can suggest such model; if it is inconsistent with the data, that would make the results far more interesting.

Morrell et al. (eLife 12, RP89337,2024 [1]) suggest a very simple model in which the whole population is driven by a slowly time-varying quantity. It would be nice to determine whether it matched this data. If it couldn’t, that would add some evidence that there is something interesting going on.

We appreciate your insightful suggestion to consider the model proposed by Morrell et al. (eLife 12, RP89337, 2024 [1]), where a slowly time-varying quantity drives the entire neural population. We conducted simulations using parameters from Morrell et al. [4, 1], as detailed below.

Our simulations show that Morrell’s model can replicate a degree of scaleinvariance when using functional sampling or RG as referred to in Morrell et al, 2021, PRL [4] (FSap, Fig.S23A-D, Author response image 1). However, it fails to fully capture the scale-invariance of collapsing spectra we observed in data under random sampling (RSap, Fig.S23E-H). This discrepancy suggests that additional dynamics or structures in the neural activity are not captured by this simple model, indicating the presence of potentially novel and interesting features in the data that merit further investigation.

Unlike random sampling, the collapse of eigenspectra under functional sampling does not require a stringent condition on the kernel function f(x) in our ERM theory (see Discussion line 269-275), potentially explaining the differing results between Fig.S23A-D and Fig.S23E-H.

We have incorporated these findings into the Result section 2.1 (lines 100-101) and Discussion section (lines 277-282, quoted below):

“Morrell et al. [4, 1] suggested a simple model in which a slow time-varying factor influences the entire neural population. To explore the effects of latent variables, we assessed if this model explains the scale invariance in our data. The model posits that neural activity is primarily driven by a few shared latent factors. Simulations showed that the resulting eigenspectra differed considerably from our findings (Fig. S23). Although the Morrell model demonstrated a degree of scale invariance under functional sampling, it did not align with the scale-invariant features under random sampling observed in our data, suggesting that this simple model might not capture all crucial features in our observations.”

Author response image 1:

Morrell’s latent model. A: We reproduce the results as presented in Morrell et al., PRL 126(11), 118302 (2021) [4]. Parameters are same as Fig. S23A. Sampled 16 to 256 neurons. Unlike in our study, the mean eigenvalues are not normalized to one. Dashed line: eigenvalues fitted to a power law. See also Morrell et al. [4] Fig.1C. Parameters are same as Author response image 1. µ is the power law exponent (black) of the fit, which is different from the µ parameter used to characterize the slow decay of the spatial correlation function, but corresponds to the parameter α in our study.

(2) The quantification of the degree of scale invariance is done using a ”collapse index” (CI), which could be better explained/motivated. The fact that the measure is computed only for the non-leading eigenvalues makes sense but it is not clear when originally introduced. How does this measure compare to other measures of the distance between distributions?

We thank you for raising this important point regarding the explanation and motivation for our Collapse Index (CI). We defined the Collapse Index (CI) instead of other measures of distance between distributions for two main reasons. First, the CI provides an intuitive quantification of the shift of the eigenspectrum motivated by our high-density theory for the ERM model (Eq. 3, Fig. 4A). This high-density theory is only valid for large eigenvalues excluding the leading ones, and hence we compute the CI measure with a similar restriction of the range of area integration. Second, when using distribution to assess the collapse (e.g., we can use kernel density method to estimate the distribution of eigenvalues and then calculate the KL divergence between the two distributions), it is necessary to first estimate the distributions. This estimation step introduces errors, such as inaccuracies in estimating the probability of large eigenvalues.

We agree that a clearer explanation would enhance the manuscript and thus have made modifications accordingly. The CI is now introduced more clearly in the Results section (lines 145-148) and further detailed in the Methods section (lines 630-636). We have also revised the CI diagram in Fig. 4A to better illustrate the shift concept using a more intuitive cartoon representation.

(3) The paper focuses on the case in which the dimensionality saturates to a finite value as the number of recorded neurons is increased. It would be useful to contrast with a case in which this does not occur. The paper would be strengthened by a comparison with Manley et al. 2024, which argued that, unlike this study, dimensionality of activity in spontaneously behaving head-fixed mice did not saturate.

Thank you for highlighting this comparison. We have included a discussion (lines 303-309) comparing our approach with Manley et al. (2024) [2]. While Manley et al. [2] primarily used shared variance component analysis (SVCA) to estimate neural dimensionality, they observed that using PCA led to dimensionality saturation (see Figure S4D, Manley et al. [2]), consistent with our findings (Fig. 2D). We acknowledge the value of SVCA as an alternative approach and agree that it is an interesting avenue for future research. In our study, we chose to use PCA for several reasons. PCA is a well-established and widely trusted method in the neuroscience community, with a proven track record of revealing meaningful patterns in neural data. Its mathematical properties are well understood, making it particularly suitable for our theoretical analysis. While we appreciate the insights that newer methods like SVCA can provide, we believe PCA remains the most appropriate tool for addressing our specific research questions.

(4) More importantly, we don’t understand why dimensionality saturates. For the rank plot given in Eq. 3,

where k is rank. Using this, one can estimate sums over eigenvalues by integrals. Focusing on the N-dependence, we have

This gives

We don’t think you ever told us what mu/d was (see point 13 below), but in the discussion you implied that it was around 1/2 (line 249). In that case, D_PR should be approximately linear in N. Could you explain why it isn’t?

Thank you for your careful derivation. Along this line of calculations you suggested, we have now added derivations on using the ERM spectrum to estimate the upper bound of the dimension in the Methods (section 4.14.4). To deduce D_PR from the spectrum, we focus on the high-density region, where an analytical expression for large eigenvalues λ is given by:

Here, d is dimension of functional space, L is the linear size of functional space, ρ is the neuron density and γ is the coefficient in Eq. (3), which only depends on d, µ and E(σ²). The primary difference between your derivation and ours is that the eigenvalue λ_r decays rapidly after the threshold r \= β(N), which significantly affects the summations and . Since we did not discuss the small eigenvalues in the article, we represent them here as an unknown function η(r,N,L).

The sum is the trace of the covariance matrix C. As emphasized in the Methods section, without changing the properties the covariance spectrum, we always consider a normalized covariance matrix such that the mean neural activity variance E(σ²) = 1. Thus

rather than

The issue stems from overlooking that Eq. (3) is valid only for large eigenvalues (λ > 1).

Using the Cauchy–Schwarz inequality, we have a upper bound of

Conversely, provides a lower bound of :

As a result, we must have

In random sampling (RSap), L is fixed. We thus must have a bounded dimensionality that is independent of N for our ERM model. In functional sampling (FSap), L varies while the neuronal density ρ is fixed, leading to a different scaling relationship of the upper bound, see Methods (section 4.14.4) for further discussion.

(5) The authors work directly with ROIs rather than attempting to separate the signals from each neuron in an ROI. It would be worth discussing whether this has a significant effect on the results.

We appreciate your thoughtful question on the potential impact of using ROIs. The use of ROIs likely does not impact our key findings since they are validated across multiple datasets with various recording techniques and animal models, from zebrafish calcium imaging to mouse brain multi-electrode recordings (see Figure S2, S24). The consistency of the scale-invariant covariance spectrum in diverse datasets suggests that ROIs in zebrafish data do not significantly alter the conclusions, and they together enhance the generalizability of our results. We highlight this in the Discussion section (lines 319-323).

(6) Does the Euclidean random matrix model allow the authors to infer the value of D or µ? Since the measured observables only depend on µ/D it seems that one cannot infer the latent dimension where distances between neurons are computed. Are there any experiments that one could, in principle, perform to measure D or mu? Currently the conclusion from the model and data is that D/µ is a large number so that the spectrum is independent of neuron density rho. What about the heterogeneity of the scales σ_i, can this be constrained by data?

Measuring d and µ in the ERM Model

We agree with you that the individual values of d and µ cannot be determined separately from our analysis. In our analysis using the Euclidean Random Matrix (ERM) model, we fit the ratio µ/d, rather than the individual values of d (dimension of the functional space) or µ (exponent of the distance-dependent kernel function). This limitation is inherent because the model’s predictions for observable quantities, such as the distribution of pairwise correlation, are dependent solely on this ratio.

Currently there are no directly targeted experiments to measure d. The dimensions of the functional space is largely a theoretical construct: it could serve to represent latent variables encoding cognitive factors that are distributed throughout the brain or specific sensory or motor feature maps within a particular brain region. It may also be viewed as the embedding space to describe functional connectivity between neurons. Thus, a direct experimental measurement of the dimensions of the functional space could be challenging. Although there are variations in the biological interpretation of the functional space, the consistent scale invariance observed across various brain regions indicates that the neuronal relationships within the functional space can be described by a uniform slowly decaying kernel function.

Regarding the Heterogeneity of σ_i

The heterogeneity of neuronal activity variances ( σ_i) is a critical factor in our analysis. Our findings indicate that this heterogeneity:

(1) Enhances scale invariance: The covariance matrix spectrum, which incorporates the heterogeneity of , exhibits stronger scale invariance compared to the correlation matrix spectrum, which imposes for all neurons. This observation is supported by both experimental data and theoretical predictions from the ERM model, particularly in the intermediate density regime.

(2) Can be constrained by data: We fit a log-normal distribution to the experimentally observed σ² values to capture the heterogeneity in our model which leads to excellent agreement with data (section 4.8.1). Figure S10 provides evidence for this by directly comparing the eigenspectra obtained from experimental data (Fig S10A-F) with those generated by the fitted ERM model (Fig S10M-R). These results suggest that the data provides valuable information about the distribution of neuronal activity variances.

In conclusion, the ERM model and our analysis cannot separately determine d and µ. We also highlight that the neuronal activity variance heterogeneity, constrained by experimental data, plays a crucial role in improving the scale invariance.

(7) Does the fitting procedure for the positions x in the latent space recover a ground truth in your statistical regime (for the number of recorded neurons)? Suppose you sampled some neurons from a Euclidean random matrix theory. Does the MDS technique the authors use recover the correct distances?

While sampling neurons from a Euclidean random matrix model, we demonstrated numerically that the MDS technique can accurately recover the true distances, provided that the true parameter f(x) is known. To quantify the precision of recovery, we applied the CCA analysis (Section 4.9) and compared the true coordinates from the original Euclidean random matrix with the fitted coordinates obtained through our MDS procedure. The CCA correlation between the true and fitted coordinates in each spatial dimension is nearly 1 (the difference from 1 is less than 10⁻⁷). When fitting with experimental data, one source of error arises from parameter estimation. To evaluate this, we assess the estimation error of the fitted parameters. When we choose µ \= 0_.5 in our ERM model and then fit the distribution of the pairwise correlation (Eq. 21), the estimated parameter is = 0.503 ± 0._007 (standard deviation). Then, we use the MDS-recovered distances to fit the coordinates with the fitted kernel function , which is determined by the fitted parameter . The CCA correlation between the true and fitted coordinates in each direction remains nearly 1 (the difference from 1 is less than 10⁻⁵).

(8) l. 49: ”... both the dimensionality and covariance spectrum remain invariant ...”. Just to be clear, if the spectrum is invariant, then the dimensionality automatically is too. Correct?

Thanks for the question. In fact, there is no direct causal relationship between eigenvalue spectrum invariance and dimensionality invariance as we elaborate below and added discussions in lines 311-317. For eigenvalue spectrum invariance, we focus on the large eigenvalues, whereas dimensionality invariance considers the second order statistics of all eigenvalues. Consequently, the invariance results for these two concepts may differ. And dimensional and spectral invariance have different requirements:

(1) The condition for dimensional saturation is finite mean square covariance

The participation ratio D_PR for random sampling (RSap) is given by Eq. 5:

This expression becomes invariant as N → ∞ if the mean square covariance is finite. In contrast, neural dynamics models, such as the balanced excitatory-inhibitory (E-I) neural network [5], exhibit a different behavior, where , leading to unbounded dimensionality (see discussion lines 291-295, section 6.9 in SI).

(2) The requirements for spectral invariance involving the kernel function

In our Euclidean Random Matrix (ERM) model, the eigenvalue distribution follows:

For spectral invariance to emerge: (1) The eigenvalue distribution must remain unchanged after sampling. (2) Since sampling reduces the neuronal density ρ. (3) The ratio µ/d must approach 0 to maintain invariance.

We can also demonstrate that D_PR is independent of density ρ in the large N limit (see the answer of question 4).

In conclusion, there is no causal relationship between spectral invariance and dimensionality invariance. This is also the reason why we need to consider both properties separately in our analysis.

(9) In Eq. 1, the exact expression, which includes i=j, isn’t a lot harder than the one with i=j excluded. So why i≠j?

The choice is for illustration purposes. In Eq. 1, we wanted to demonstrate that the dimension saturates to a value independent of N. When dividing the numerator and denominator of this expression by N², the term is independent of the neuron number N, but the term associated with the diagonal entries is of order O(1_/N_) and can be ignored for large N.

(10) Fig. 2D: Could you explain where the theory line comes from?

We first estimate ] from all neurons, and then compute D_PR for different neuron numbers N using Eq.5 (). This is further clarified in lines 511-512.

(11) l 94-5: ”It [scale invariance] is also absent when replacing the neural covariance matrix eigenvectors with random ones, keeping the eigenvalues identical (Fig. 2H).” If eigenvalues are identical, why does the spectrum change?

The eigenspectra of the covariance matrices in full size are the same by construction, but the eigenspectra of the sampled covariance matrices are different because the eigenvectors affect the sampling results. Please also refer to the construction process described in section 4.3 where this is also discussed: “The composite covariance matrix with substituted eigenvectors in (Fig. 2H) was created as described in the following steps. First, we generated a random orthogonal matrix U<sub>r<.sup> (based on the Haar measure) for the new eigenvectors. This was achieved by QR decomposition A=U_rR of a random matrix A with i.i.d. entries A_ij ∼ N(0_,1/N_). The composite covariance matrix C_r was then defined as, where Λ is a diagonal matrix that contains the eigenvalues of C. Note that since all the eigenvalues are real and U_r is orthogonal, the resulting C_r is a real and symmetric matrix. By construction, C_r and C have the same eigenvalues, but their sampled eigenspectra can differ.”

(12) Eq 3: There’s no dependence on the distribution of sigma. Is that correct?

Indeed, this is true in the high-density regime when the neuron density ρ is large. The p(λ) depends only on E(σ²) rather than the distribution of σ (see Eq. 8). However, in the intermediate density regime, p(λ) depends on the distribution of σ (see Eq.9 and Eq.10). In our analysis, we consider E(σ⁴) as a measure of heterogeneity.

(13) Please tell us the best fit values of µ/d.

This information now is added in the figure caption of Fig S10: µ/d \= [0_.456,0.258,0.205,0.262,0.302,0._308] in fish 1-6.

(14) l 133: ”The eigenspectrum is rho-independent whenever µ/d ≈ 0.”

It looks to me like rho sets the scale but not the shape. Correct? If so, why do we care about the overall scale – isn’t it the shape that’s important?

Yes, our study focuses on the overall scale not only the shape, because many models, such as the ERM with other kernel functions, random RNNs, Morrell’s latent model [4, 1], can exhibit a power-law spectrum. However, these models do not exhibit scale-invariance in terms of spectrum curve collapsing. Therefore, considering the overall scale reveal additional non-trivial phenomenon.

(15) Figs. 3 and 4: Are the grey dots the same as in previous figures? Either way, please specify what they are in the figure caption.

Yes, they are the same, and thank you for pointing it out. It has been specified in the figure caption now.

(16) Fig. 4B: Top is correlation matrix, bottom is covariance matrix, correct? If so, that should be explicit. If not, it should be clear what the plots are.

That is correct. Both matrices (correlation - top, covariance - bottom) are labeled in the figure caption and plot (text in the lower left corner).

(17) l 158: ”First, the shape of the kernel function f(x) over a small distance ...”. What does ”over a small distance” mean?

We thank you for seeking clarification on this point. We understand that the phrase ”over a small distance” could be made clearer. We made a revised explanation in lines 164-165 Here, “over a small distance” refers to modifications of the particular kernel function f(x) we use Eq. 11 near x \= 0 in the functional space, while preserving the overall power-law decay at larger distances. The t-distribution based f(x) (Eq. 11) has a natural parameter ϵ that describes the transition to near 0. So we modified f(x) in different ways, all within this interval of |x| ≤ ϵ, and considered different values of ϵ. Table S3 and Figure S7 provide a summary of these modifications. Figure S7 visually compares these modifications to the standard power-law kernel function, highlighting the differences in shape near x \= 0.

Our findings indicate that these alterations to the kernel function at small distances do not significantly affect the distribution of large eigenvalues in the covariance spectrum. This supports our conclusion that the large eigenvalues are primarily determined by the slow decay of the kernel function at larger distances in the functional space, as this characteristic governs the overall correlations in neural activity.

(18) l390 . This x_i is, we believe, different from the x_i which is position in feature space. Given the difficulty of this paper, it doesn’t help to use the same symbol to mean two different things. But maybe we’re wrong?

Thank you for your careful reading and suggestion. Indeed here x_i was representing activity rather than feature space position. We have thus revised the notation (Line 390 has been updated to line 439 as well.):

In this revised notation: a_i(t) represents the neural activity of neuron i at time t (typically the firing rate we infer from calcium imaging). is simply the mean activity of neuron i across time. Meanwhile, we’ll keep x_i exclusively for denoting positions in the functional space.

This change should make it much easier to distinguish between neural activity measurements and spatial coordinates in the functional space.

(19) Eq. 19: is it correct that g(u) is not normalized to 1? If so, does that matter?

It is correct that the approximation of g(u) is not normalized to 1, as Eq. 19 provides an approximation suitable only for small pairwise distances (i.e., large correlation). Therefore, we believe this does not pose an issue. We have newly added this note in lines 691-693.

(20) I get a different answer in Eq. 20:

Whereas in Eq. 20,

µ

Which is correct?

Thank you for your careful derivation. We believe the difference arises in the calculation of g(u).In our calculations:

,

(Your first equation seems to missed an 1_/µ_ in R’s exponent.)

,

That is, Eq. 20 is correct. From these, we obtain

rather than

We hope this clarifies the question.

(21) I’m not sure we fully understand the CCA analysis. First, our guess as to what you did: After sampling (either Asap or Fsap), you used ERM to embed the neurons in a 2-D space, and then applied canonical correlation analysis (CCA). Is that correct? If so, it would be nice if that were more clear.

We first used ERM to embed all the neurons in a 2-D functional space, before any sampling. Once we have the embedding, we can quantify how similar the functional coordinates are with the anatomical coordinates using R_CCA (section 2.4). We can then use the anatomical and functional coordinates to perform ASap and FSap, respectively. Our theory in section 2.4 predicts the effect on dimension under these samplings given the value of R_CCA estimated earlier (Fig. 5D). The detailed description of the CCA analysis is in section 4.9, where we explain how CCA is used to find the axes in both anatomical and functional spaces that maximize the correlation between projections of neuron coordinates.

As to how you sampled under Fsap, I could not figure that out – even after reading supplementary information. A clearer explanation would be very helpful.

Thank you for your feedback. Functional sampling (FSap) entails the expansion of regions of interest (ROIs) within the functional space, as illustrated in Figure 5A, concurrently with the calculation of the covariance matrix for all neurons contained within the ROI. Technically, we implemented the sampling using the RG approach [6], which is further elaborated in Section 4.12 (lines 852-899), quoted below.

Stage (i): Iterative Clustering We begin with N</sub>0</sub> neurons, where N</sub>0</sub> is assumed to be a power of 2. In the first iteration, we compute Pearson’s correlation coefficients for all neuron pairs. We then search greedily for the most correlated pairs and group the half pairs with the highest correlation into the first cluster; the remaining neurons form the second cluster. For each pair (a,b), we define a coarse-grained variable according to:

,

Where normalizes the average to ensure unit nonzero activity. This process reduces the number of neurons to N₁ = N₀/2. In subsequent iterations, we continue grouping the most correlated pairs of the coarse-grained neurons, iteratively reducing the number of neurons by half at each step. This process continues until the desired level of coarse-graining is achieved.

When applying the RG approach to ERM, instead of combining neural activity, we merge correlation matrices to traverse different scales. During the _k_th iteration, we compute the coarse-grained covariance as:

and the variance as:

Following these calculations, we normalize the coarse-grained covariance matrix to ensure that all variances are equal to one. Note that these coarse-grained covariances are only used in stage (i) and not used to calculate the spectrum.

Stage (ii): Eigenspectrum Calculation The calculation of eigenspectra at different scales proceeds through three sequential steps. First, for each cluster identified in Stage (i), we compute the covariance matrix using the original firing rates of neurons within that cluster (not the coarse-grained activities). Second, we calculate the eigenspectrum for each cluster. Finally, we average these eigenspectra across all clusters at a given iteration level to obtain the representative eigenspectrum for that scale.

In stage (ii), we calculate the eigenspectra of the sub-covariance matrices across different cluster sizes as described in [6]. Let N₀ = 2<sup>n</sub> be the original number of neurons. To reduce it to size N \= N₀/2^k = 2^n-k, where k is the kth reduction step, consider the coarse-grained neurons in step n − k in stage (i). Each coarse-grained neuron is a cluster of 2^n-k neurons. We then calculate spectrum of the block of the original covariance matrix corresponding to neurons of each cluster (there are 2^k such blocks). Lastly, an average of these 2^k spectra is computed.

For example, when reducing from N₀ = 2³ = 8 to N \= 2³⁻¹ = 4 neurons (k \= 1), we would have two clusters of 4 neurons each. We calculate the eigenspectrum for each 4x4 block of the original covariance matrix, then average these two spectra together. To better understand this process through a concrete example, consider a hypothetical scenario where a set of eight neurons, labeled 1,2,3,...,7,8, are subjected to a two-step clustering procedure. In the first step, neurons are grouped based on their maximum correlation pairs, for example, resulting in the formation of four pairs: {1,2},{3,4},{5,6}, and {7,8} (see Fig. S22). Subsequently, the neurons are further grouped into two clusters based on the results of the RG step mentioned above. Specifically, if the correlation between the coarse-grained variables of the pair {1,2} and the pair {3,4} is found to be the largest among all other pairs of coarse-grained variables, the first group consists of neurons {1,2,3,4}, while the second group contains neurons {5,6,7,8}. Next, take the size of the cluster N = 4 for example. The eigenspectra of the covariance matrices of the four neurons within each cluster are computed. This results in two eigenspectra, one for each cluster. The correlation matrices used to compute the eigenspectra of different sizes do not involve coarse-grained neurons. It is the real neurons 1,2,3,...,7,8, but with expanding cluster sizes. Finally, the average of the eigenspectra of the two clusters is calculated.

(22) Line 37: ”even if two cell assemblies have the same D_PR, they can have different shapes.” What is meant by shape here isn’t clear.

Thank you for pointing out this potential ambiguity. The “shape” here refers to the geometric configuration of the neural activity space characterized as a highdimensional ellipsoid by the covariance. Specifically, if we denote the eigenvalues of the covariance matrix as λ₁,λ₂,...,λ_N, then corresponds to the length of the i-th semi-axis of this ellipsoid (Figure 1B). As shown in Figure 1C, two neural populations with the same dimensionality (D_PR = 25/11 ≈ 2.27) exhibit different eigenvalue spectra, leading to differently shaped ellipsoids. This clarification is now included in lines 39-40.

(23) Please discuss if any information about the latent dimension or kernel function can be inferred from the measurements.

Same as comment(6): we would like to clarify that in our analysis using the Euclidean Random Matrix (ERM) model, we fit the ratio µ/d, rather than the individual values of d (dimension of the functional space) or µ (exponent of the distancedependent kernel function). This limitation is inherent because the model’s predictions for observable quantities, such as the eigenvalue spectrum of the covariance matrix, are dependent solely on this ratio.

For the kernel function, once the d is chosen, we can infer the general shape of the kernel function from data (Figs S12 and S13), up to a certain extent (see also lines 164-166). In particular, we can compare the eigenspectrum of the simulation results for different kernel functions with the eigenspectrum of our data. This allows us to qualitatively exclude certain kernel functions, such as the exponential and Gaussian kernels (Fig. S4), which show clear differences from our data.

References

(1) M. C. Morrell, I. Nemenman, A. Sederberg, Neural criticality from effective latent variables. eLife 12, RP89337 (2024).

(2) J. Manley, S. Lu, K. Barber, J. Demas, H. Kim, D. Meyer, F. M. Traub, A. Vaziri, Simultaneous, cortex-wide dynamics of up to 1 million neurons reveal unbounded scaling of dimensionality with neuron number. Neuron (2024).

(3) S. A. Moosavi, S. S. R. Hindupur, H. Shimazaki, Population coding under the scale-invariance of high-dimensional noise (2024).

(4) M. C. Morrell, A. J. Sederberg, I. Nemenman, Latent dynamical variables produce signatures of spatiotemporal criticality in large biological systems. Physical Review Letters 126, 118302 (2021).

(5) A. Renart, J. De La Rocha, P. Bartho, L. Hollender, N. Parga, A. Reyes, K. D. Harris, The asynchronous state in cortical circuits. science 327, 587–590 (2010).

(6) L. Meshulam, J. L. Gauthier, C. D. Brody, D. W. Tank, W. Bialek, Coarse graining, fixed points, and scaling in a large population of neurons. Physical Review Letters 123, 178103 (2019).

Author Response

We thank you for the time you took to review our work and for your feedback!

The major changes to the manuscript are:

1. We have extended the range of locomotion velocity over which we compare its dependence with cholinergic activity in Figures 2E and S2H.

2. We have quantified the contributions of cholinergic stimulation on multiplicative and additive gains on visual responses (Figure S7).

3. We have provided single cell examples for the change in latency to visual response (Figure S12).

4. We have added an analysis to compare layer 2/3 and layer 5 locomotion onset responses as a function of visuomotor condition (Figure S8).

A detailed point-by-point response to all reviewer concerns is provided below.  

Reviewer #1 (Public Review):

The paper submitted by Yogesh and Keller explores the role of cholinergic input from the basal forebrain (BF) in the mouse primary visual cortex (V1). The study aims to understand the signals conveyed by BF cholinergic axons in the visual cortex, their impact on neurons in different cortical layers, and their computational significance in cortical visual processing. The authors employed two-photon calcium imaging to directly monitor cholinergic input from BF axons expressing GCaMP6 in mice running through a virtual corridor, revealing a strong correlation between BF axonal activity and locomotion. This persistent activation during locomotion suggests that BF input provides a binary locomotion state signal. To elucidate the impact of cholinergic input on cortical activity, the authors conducted optogenetic and chemogenetic manipulations, with a specific focus on L2/3 and L5 neurons. They found that cholinergic input modulates the responses of L5 neurons to visual stimuli and visuomotor mismatch, while not significantly affecting L2/3 neurons. Moreover, the study demonstrates that BF cholinergic input leads to decorrelation in the activity patterns of L2/3 and L5 neurons.

This topic has garnered significant attention in the field, drawing the interest of many researchers actively investigating the role of BF cholinergic input in cortical activity and sensory processing. The experiments and analyses were thoughtfully designed and conducted with rigorous standards, leading to convincing results which align well with findings in previous studies. In other words, some of the main findings, such as the correlation between cholinergic input and locomotor activity and the effects of cholinergic input on V1 cortical activity, have been previously demonstrated by other labs (Goard and Dan, 2009; Pinto et al., 2013; Reimer et al., 2016). However, the study by Yogesh and Keller stands out by combining cutting-edge calcium imaging and optogenetics to provide compelling evidence of layerspecific differences in the impact of cholinergic input on neuronal responses to bottom-up (visual stimuli) and top-down inputs (visuomotor mismatch).

We thank the reviewer for their feedback.

Reviewer #2 (Public Review):

The manuscript investigates the function of basal forebrain cholinergic axons in mouse primary visual cortex (V1) during locomotion using two-photon calcium imaging in head-fixed mice. Cholinergic modulation has previously been proposed to mediate the effects of locomotion on V1 responses. The manuscript concludes that the activity of basal forebrain cholinergic axons in visual cortex provides a signal which is more correlated with binary locomotion state than locomotion velocity of the animal. Cholinergic axons did not seem to respond to grating stimuli or visuomotor prediction error. Optogenetic stimulation of these axons increased the amplitude of responses to visual stimuli and decreased the response latency of layer 5 excitatory neurons, but not layer 2/3 neurons. Moreover, optogenetic or chemogenetic stimulation of cholinergic inputs reduced pairwise correlation of neuronal responses. These results provide insight into the role of cholinergic modulation to visual cortex and demonstrate that it affects different layers of visual cortex in a distinct manner. The experiments are well executed and the data appear to be of high quality. However, further analyses are required to fully support several of the study's conclusions.

We thank the reviewer for their feedback.

1) In experiments analysing the activity of V1 neurons, GCaMP6f was expressed using a ubiquitous Ef1a promoter, which is active in all neuronal cell types as well as potentially non-neuronal cells. The manuscript specifically refers to responses of excitatory neurons but it is unclear how excitatory neuron somata were identified and distinguished from that of inhibitory neurons or other cell types.

This might be a misunderstanding. The Ef1α promoter has been reported to drive highly specific expression in neurons (Tsuchiya et al., 2002) with 99.7% of labeled cells in layer 2/3 of rat cortex being NeuN+ (a neuronal marker), with only 0.3% of labeled cells being GFAP+ (a glial marker) (Yaguchi et al., 2013). This bias was even stronger in layer 5 with 100% of labeled cells being NeuN+ and none GFAP+ (Yaguchi et al., 2013). The Ef1α promoter in an AAV vector, as we use it here, also biases expression to excitatory neurons. In layer 2/3 of mouse visual cortex, we have found that 96.8% ± 0.7% of labeled neurons are excitatory three weeks after viral injection (Attinger et al., 2017). Similar results have also been found in rats (Yaguchi et al., 2013), where on expressing GFP under Ef1a promoter delivered using Lenti virus, 95.2% of labeled neurons in layer 2/3 were excitatory and 94.1% in layer 5 were excitatory. These numbers are comparable to the ones obtained with promoters commonly used to target expression to excitatory neurons. To do this, typically two variants of promoters based on the transcription start region of CaMKIIα gene have been used. The first, the CaMKIIα-0.4 promoter, results in 95% excitatory specificity (Scheyltjens et al., 2015). The second, the CaMKIIα-1.3 promoter, results in only 82% excitatory specificity (Scheyltjens et al., 2015), and is thus not far from chance. We have clarified this in the manuscript. Nevertheless, we have removed the qualifier “excitatory” when talking about neurons in most instances, throughout the manuscript.

2) The manuscript concludes that cholinergic axons convey a binary locomotion signal and are not tuned to running speed. The average running velocity of mice in this study is very slow - slower than 15 cm/s in the example trace in Figure 1D and speeds <6 cm/s were quantified in Figure 2E. However, mice can run at much faster speeds both under head-fixed and freely moving conditions (see e.g. Jordan and Keller, 2020, where example running speeds are ~35 cm/s). Given that the data in the present manuscript cover such a narrow range of running speeds, it is not possible to determine whether cholinergic axons are tuned to running speed or convey a binary locomotion signal.

Our previous analysis window of 0-6.25 cm/s covered approximately 80% of all data. We have increased the analysis window to 0-35 cm/s that now covers more than 99% of the data (see below). Also, note that very high running speeds are probably overrepresented in the Jordan and Keller 2020 paper as mice had to be trained to run reliably before all experiments given the relatively short holding times of the intracellular recordings. The running speeds in our current dataset are comparable to other datasets we have acquired in similar experiments.

Figure 2E has now been updated to reflect the larger range of data. Please note, as the number of mice that contribute to the data now differs as a function of velocity (some mice run faster than others), we have now switched to a variant of the plot based on hierarchical bootstrap sampling (see Methods). This does not overtly change the appearance of the plot. See Author response image 1 for a comparison of the original plot, the extended range without bootstrap sampling, and the extended range with bootstrap sampling currently used in the paper.

Author response image 1.

Average activity of cholinergic axons as a function of locomotion velocity. (A) As in the previous version of the manuscript. (B) As in A, but with the extended velocity range. (C) As in B, but using hierarchical bootstrap sampling to estimate median (red dots) and 95% confidence interval (shading) for each velocity bin.

3) The analyses in Figure 4 only consider the average response to all grating orientations and directions. Without further analysing responses to individual grating directions it is unclear how stimulation of cholinergic inputs affects visual responses. Previous work (e.g. Datarlat and Stryker, 2017) has shown that locomotion can have both additive and multiplicative effects and it would be valuable to determine the type of modulation provided by cholinergic stimulation.

We thank the reviewer for this suggestion. To address this, we quantified how cholinergic stimulation influenced the orientation tuning of V1 neurons. The stimuli we used were full field sinusoidal drifting gratings of 4 different orientations (2 directions each). For each neuron, we identified the preferred orientation and plotted responses relative to this preferred orientation as a function of whether the mouse was running, or we were stimulating cholinergic axons. Consistent with previous work, we found a mixture of a multiplicative and an additive components during running. With cholinergic axon stimulation, the multiplicative effect was stronger than the additive effect. This is now quantified in Figure S7.

4) The difference between the effects of locomotion and optogenetic stimulation of cholinergic axons in Figure 5 may be confounded by differences in the visual stimulus. These experiments are carried out under open-loop conditions, where mice may adapt their locomotion based on the speed of the visual stimulus. Consequently, locomotion onsets are likely to occur during periods of higher visual flow. Since optogenetic stimulation is presented randomly, it is likely to occur during periods of lower visual flow speed. Consequently, the difference between the effect of locomotion and optogenetic stimulation may be explained by differences in visual flow speed and it is important to exclude this possibility.

We find that in general locomotion is unaffected by visual flow in open loop conditions in this type of experiment (in this particular dataset, there was a small negative correlation between locomotion and visual flow in the open loop condition, Author response image 2).

Author response image 2.

Correlation between visual flow and locomotion in open loop conditions. Average correlation of locomotion velocity and visual flow speed in open loop for all mice in Figure 5. Each dot is an imaging site. In the open loop, the correlation between locomotion and visual flow speed is close to zero, but significantly negative in this dataset.

However, to directly address the concern that our results are influenced by visual flow, we can restrict our analysis only to locomotion onsets that occurred in absence of visual flow (Author response image 3A and R3B). These responses are not substantially different from those when including all data (Figures 5A and 5B). Thus, the difference between the effect of locomotion and optogenetic stimulation cannot be explained by differences in visual flow speed.

Author response image 3.

Open loop locomotion onset responses without visual flow. (A) Average calcium response of layer 2/3 neurons in visual cortex to locomotion onset in open loop in the absence of visual flow. Shading indicates SEM. (B) As in A, but for layer 5 neurons.

5) It is unclear why chemogenetic manipulations of cholinergic inputs had no effect on pairwise correlations of L2/3 neuronal responses while optogenetic stimulation did.

This is correct – we do not know why that is the case and can only speculate. There are at least two possible explanations for this difference:

1) Local vs. systemic. The optogenetic manipulation is relatively local, while the chemogenetic manipulation is systemic. It is not clear how cholinergic release in other brain regions influences the correlation structure in visual cortex. It is conceivable that a cortex-wide change in cholinergic release results in a categorically different state with a specific correlation structure in layer 2/3 neurons different from the one induced by the more local optogenetic manipulation.

2) Layer-specificity of activation. Cholinergic projections to visual cortex arrive both in superficial and deep layers. We activate the axons in visual cortex optogenetically by illuminating the cortical surface. Thus, in our optogenetic experiments, we are primarily activating the axons arriving superficially, while in the chemogenetic experiment, we are likely influencing superficial and deep axons similarly. Thus, we might expect a bias in the optogenetic activation to influencing superficial layers more strongly than the chemogenetic activation does.

6) The effects of locomotion and optogenetic stimulation on the latency of L5 responses in Figure 7 are very large - ~100 ms. Indeed, typical latencies in mouse V1 measured using electrophysiology are themselves shorter than 100 ms (see e.g. Durand et al., 2016). Visual response latencies in stationary conditions or without optogenetic stimulation appear surprisingly long - much longer than reported in previous studies even under anaesthesia. Such large and surprising results require careful analysis to ensure they are not confounded by artefacts. However, as in Figure 4, this analysis is based only on average responses across all gratings and no individual examples are shown.

This is correct and we speculate this is the consequence of a combination of different reasons.

1) Calcium imaging is inherently slower than electrophysiological recordings. While measuring spiking responses using electrophysiology, response latencies of on the order of 100 ms have indeed been reported, as the reviewer points out. Using calcium imaging these latencies are typically 4 times longer (Kuznetsova et al., 2021). This is likely a combination of a) calcium signals that are slower than electrical changes, b) delays in the calcium sensor itself, and c) temporal sampling used for imaging that is about 3 orders of magnitude slower than what typically used for electrophysiology.

2) Different neurons included in analysis. The calcium imaging likely has very different biases than electrophysiological recordings. Historically, the fraction of visually responsive neurons in visual cortex based on extracellular electrophysiological recordings has been systematically overestimated (Olshausen and Field, 2005). One key contributor to this is the fact that recordings are biased to visually responsive neurons. The criteria for inclusion of “responsive neurons” strongly influences the “average” response latency. In addition, calcium imaging has biases that relate to the vertical position of the somata in cortex. Both layer 2/3 and layer 5 recordings are likely biased to superficial layer 2/3 and superficial layer 5 neurons. Conversely, electrical recordings are likely biased to layer 4 and layer 5 neurons. Thus, comparisons at this level of resolution between data obtained with these two methods are difficult to make.

We have added example neurons as Figure S12, as suggested.  

Reviewer #1 (Recommendations For The Authors):

While the study showcases valuable insights, I have a couple of concerns regarding the novelty of their research and the interpretation of results. By addressing these concerns, the authors can clarify the positioning of their research and strengthen the significance of their findings.

(Major comments)

1) Page 1, Line 21: The authors claim, "Our results suggest that acetylcholine augments the responsiveness of layer 5 neurons to inputs from outside of the local network, enabling faster switching between internal representations during locomotion." However, it is not clear which specific data or results support the claim of "switching between internal representations." Overall, their study primarily presents responses averaged across all neurons imaged, lacking a detailed exploration of individual neuron response patterns. Population analysis, such as PCA and decoding, can be used to assess the encoding of each stimulus by V1 neurons - "internal representation."<br /> To strengthen their claim regarding "switching between internal representations," the authors could consider an experiment measuring the speed at which the population activity pattern A transitions to the population activity pattern B when the visual stimulus switches from A to B. Such experiments would significantly enhance the impact of their study, providing a clearer understanding of how BF cholinergic input influences the dynamic representation of stimuli during locomotion.

We thank the reviewer for bringing this up. That acetylcholine enables a faster switching between internal representations in layer 5 is a speculation. We have attempted to make this clearer in the discussion. Our speculation is based on the finding that the population response in layer 5 to sensory input is faster under high levels of acetylcholine (Figures 4D and 7B). In line with the reviewer’s intuition, the neuronal response to a change in visual stimulus, in our experiment from a uniform grey visual stimulus to a sinusoidal grating stimulus, is indeed faster. Based on evidence in favor of layer 5 encoding internal representation (Heindorf and Keller, 2023; Keller and Mrsic-Flogel, 2018; Suzuki and Larkum, 2020), we interpret the decrease in latency of the population response as a faster change in internal representation. We are not sure a decoding analysis would add much to this, given that a trivial decoder simply based on mean population response would already find a faster transition. We have expanded on our explanation of these points in the manuscript.

2) Page 4, Line 103: "..., a direct measurement of the activity of cholinergic projection from basal forebrain to the visual cortex during locomotion has not been made." This statement is incorrect. An earlier study by Reimer et al. indeed imaged cholinergic axons in the visual cortex of mice running on a wheel. They found that "After walking onset, ... ACh activation, and a large pupil diameter, were sustained throughout the walking period in both cortical areas V1 and A1." Their findings are very similar to the results presented by Yogesh and Keller - that is, BF cholinergic axons exhibited locomotion statedependent activity. The authors should clarify the positioning of this study relative to previous studies.

Reimer, J., McGinley, M., Liu, Y. et al. Pupil fluctuations track rapid changes in adrenergic and cholinergic activity in cortex. Nat Commun 7, 13289 (2016). https://doi.org/10.1038/ncomms13289

We have clarified this as suggested. However, we disagree slightly with the reviewer here. The key question is whether the cholinergic axons imaged originate in basal forebrain. While Reimer et al. 2016 did set out to do this, we believe a number of methodological considerations prevent this conclusion:

1) In their analysis, Reimer et al. 2016 combine data from mice with cholinergic axons labeled with either viral injection to basal forebrain or germline cross of ChAT-cre mice with reporter line. Unfortunately, it is unclear what the exact number of mice labeled with either strategy was. Based on the information in the paper, we can conclude that of the 6 mice used for experiments between 2 and 5 were germline cross. The problem with germline labeling of ChAT positive neurons is that when using a cross, VIP-ChAT+ neurons in cortex are also labeled. Based on the fact that Reimer et al. 2016 find an anticipatory increase in activity on locomotion onset, that is also seen by Larsen et al. 2018 (they use a germline cross strategy), an effect we do not see in our data, we speculate that a significant part of the signals reported in the Reimer et al. 2016 paper are from local VIP-ChAT+ neurons.

2) In their analysis, Reimer et al. 2016 also combine all imaging data obtained from both primary auditory cortex and primary visual cortex. Given the heterogeneity in the basal forebrain cholinergic neuronal population and their projection selectivity, to better understand these signals, it’s important to acquire the signals from cholinergic axons selectively in specific cortical regions, which we do in visual cortex. Based on the information provided in their paper, we were unfortunately not able to discern the injection location for their viral labeling strategy. Given the topographic selectivity in projection from basal forebrain, this could give hints as to the relative contribution of cholinergic projections to A1 vs V1 in their data. The injection coordinates given in the methods of the Reimer paper, of 4 mm lateral and 0.5 mm posterior to bregma to target basal forebrain, are likely wrong (they fall outside the head of the mouse).

Given the heterogeneity in the basal forebrain cholinergic neuronal population and their projection selectivity, to better understand these signals, it’s important to acquire the signals from cholinergic axons both selectively in a cortical region, as we do in visual cortex, and purely originating from basal forebrain. Collins et al. 2023 inject more laterally and thus characterize cholinergic input to S1 and A1, while Lohani et al. 2022 use GRAB sensors which complement our findings. Please note, we don’t think there is any substantial disagreement in the results of previous studies and ours, with very few exceptions, like the anticipatory increase in cholinergic activity that precedes locomotion onset in the Reimer et al. 2016 data, but not in ours. This is a rather critical point in the context of the literature of motor-related neuronal activity in mouse V1. Based on early work on the topic, it is frequently assumed that motor-related activity in V1 is driven by a cholinergic input. This is very likely incorrect given our results, hence we feel it is important to highlight this methodological caveat of earlier work.

3) Fig. 4H: The authors found that L5 neurons exhibit positive responses at the onset of locomotion in a closed-loop configuration. Moreover, these responses are further enhanced by photostimulation of BF axons.

In a previous study from the same authors' group (Heindorf and Keller, 2023), they reported 'negative' responses in L5a IT neurons during closed-loop locomotion. This raises a question about the potential influence of different L5 neuron types on the observed results between the two studies. Do the author think that the involvement of the other neuronal type in L5, the PT neurons, might explain the positive responses seen in the present study? Discussing this point in the paper would provide valuable insights into the underlying mechanisms.

Yes, we do think the positive response observed on locomotion onset in closed loop is due to non-Tlx3+ neurons. Given that Tlx3-cre only labels a subset of inter-telencephalic (IT) neurons (Gerfen et al., 2013; Heindorf and Keller, 2023), it’s not clear whether the positive response is explained by the pyramidal tract (PT) neurons, or the non-Tlx3+ IT neurons. Dissecting the response profiles of different subsets of layer 5 neurons is an active area of research in the lab and we hope to be able to answer these points more comprehensively in future publications. We have expanded on this in the discussion as suggested.

Furthermore, it would be valuable to investigate whether the effects of photostimulation of BF axons vary depending on neuronal responsiveness. This could help elucidate how neurons with positive responses, potentially putative PT neurons, differ from neurons with negative responses, putative IT neurons, in their response to BF axon photostimulation during locomotion.

We have attempted an analysis of the form suggested. In short, we found no relationship between a neuron’s response to optogenetic stimulation of ChAT axons and its response to locomotion onset, or its mean activity. Based on their response to locomotion onset in closed loop, we split layer 5 neurons into three groups, 30% most strongly decreasing (putative Tlx3+), 30% most strongly increasing, and the rest. We did not see a response to optogenetic stimulation of basal forebrain cholinergic axons in any of the three groups (Author response image 4A). We also found no obvious relationship between the mean activity of neurons and their response to optogenetic stimulation (Author response image 4B).

Author response image 4.

Neither putative layer 5 cell types nor neuronal responsiveness correlates with the response to optogenetic stimulation of cholinergic axons. (A) Average calcium response of layer 5 neurons split into putative Tlx3 (closed loop locomotion onset suppressed) and non-Tlx3 like (closed loop locomotion onset activated) to optogenetic stimulation of cholinergic axons. (B) Average calcium response of layer 5 neurons to optogenetic stimulation of cholinergic axons as a function of their mean response throughout the experimental session. Left: Each dot is a neuron. Right: Average correlation in the response of layer 5 to optogenetic stimulation and mean activity over all neurons per imaging site. Each dot is an imaging site.

(Minor comments)

1) It is unclear which BF subregion(s) were targeted in this study.

Thanks for pointing this out. We targeted the entire basal forebrain (medial septum, vertical and horizontal limbs of the diagonal band, and nucleus basalis) with our viral injections. All our axonal imaging data comes from visual cortex and given the sensory modality-selectivity of cholinergic projections to cortex, the labeled axons originate from medial septum and the diagonal bands (Kim et al., 2016). We have now added the labels for basal forebrain subregions targeted next to the injection coordinates in the manuscript.

2) Page 43, Line 818: The journal name of the cited paper Collins et al. is missing.

Fixed.

3) In the optogenetic experiments, how long is the inter-trial interval? Simulation of BF is known to have long-lasting effects on cortical activity and plasticity. It is, therefore, important to have a sufficient interval between trials.

The median inter-trial interval for different stimulation events are as follows:

• Optogenetic stimulation only : 15 s

• Optogenetic stimulation + grating : 12 s

• Optogenetic stimulation + mismatch: 35 s

• Optogenetic stimulation + locomotion onset: 45 s

We have added this information to the methods in the manuscript.

Assuming locomotion is the primary driver of acetylcholine release (as we argue in Figures 1 and 2), the frequency of stimulation roughly corresponds to the frequency of acetylcholine release experienced endogenously. It is of course possible that being awake and mobile puts the entire system in a longlasting acetylcholine driven state different from what would be observed during long-term quite wakefulness or during sleep. But the main focus of the optogenetic stimulation experiments we performed was to investigate the consequences of the rapid acetylcholine release driven by locomotion.

4) Page 11, Line 313: "..., we cannot exclude the possibility of a systemic contribution to the effects we observe through shared projections between different cortical and subcortical target." This possibility can be tested by examining the effect of optogenetic stimulation of cholinergic axons on locomotor activity, as they did for the chemogenetic experiments (Fig. S7). If the optogenetic manipulation changes locomotor activity, it is likely that this manipulation has some impact on subcortical activity and systemic contribution to the changes in cortical responses observed.

Based on the reviewer suggestion we tested this and found no change in the locomotor activity of the mice on optogenetic stimulation of cholinergic axons locally in visual cortex (we have added this as Figure S5 to the manuscript). Please note however, we can of course not exclude a systemic contribution based on this.

5) Fig. 4 and 5: In a closed-loop configuration, L2/3 neurons exhibit a transient increase in response at the onset of locomotion, while in an open-loop configuration, their response is more prolonged. On the other hand, L5 neurons show a sustained response in both configurations. Do the authors have any speculation on this difference?

This is correct. Locomotion onset responses in layer 2/3 are strongly modulated by whether the locomotion onset occurs in closed loop or open loop configurations (Widmer et al., 2022). This difference is absent in our layer 5 data here. We suspect this is a function of a differential within-layer cell type bias in the different recordings. In the layer 2/3 recordings we are likely biased strongly towards superficial L2/3 neurons that tend to be negative prediction error neurons (top-down excited and bottom-up inhibited), see e.g. (O’Toole et al., 2023). A reduction of locomotion onset responses in closed loop is what one would expect for negative prediction error neurons. While layer 5 neurons exhibit mismatch responses, they do not exhibit opposing top-down and bottom-up input that would result in such a suppression (Jordan and Keller, 2020).

We can illustrate this by splitting all layer 2/3 neurons based on their response to gratings and to visuomotor mismatch into a positive prediction error (PE) type (top 30% positive grating response), a negative prediction error type (top 30% positive visuomotor mismatch response), and the rest (remaining neurons and neurons responsive to both grating and visuomotor mismatch). Plotting the response of these neurons to locomotion onset in closed loop and open loop, we find that negative PE neurons have a transient response to locomotion onset in closed loop while positive PE neurons have a sustained increase in response in closed loop. In open loop the response of the two populations is indistinguishable. Splitting the layer 5 neurons using the same criteria, we don’t find a striking difference between closed and open loop between the two groups of neurons. We have added this as Figure S8.

Reviewer #2 (Recommendations For The Authors):

Major concerns:

1) As a ubiquitous promoter was used to drive GCaMP expression, please explain how excitatory neurons were identified.

2) As the data cover a very small range of running speeds, it is important to confirm that the binary locomotion signal model still applies when mice run at higher speeds - either by selecting recordings where mice have a wider range of running speeds or conducting additional experiments. In addition, please show the running speed tuning of individual axons.

3) Please provide a more detailed analysis of the effects of locomotion and cholinergic modulation on visual responses. How does cholinergic modulation affect orientation and direction tuning? Are the effects multiplicative or additive? How does this compare to the effects of locomotion on single neurons?

4) To ensure that the analyses in Figure 5 are not confounded by differences in the visual stimulus, please include average visual flow speed traces for each condition.

5) Please clarify why chemogenetic manipulations of cholinergic inputs had no effect on pairwise correlations in L2/3.

6) The latency effect is quite an extraordinary claim and requires careful analysis. Please provide examples of single neurons illustrating the latency effect - including responses across individual grating orientations/directions. One possible confound is that grating presentation could itself trigger locomotion or other movements. In the stationary / noOpto conditions, the grating response might not be apparent in the average trace until the animal begins to move. Thus the large latency in the stationary / noOpto conditions may reflect movement-related rather than visual responses.

Please see our responses to these points in the public review part above.

There are some minor points where text and figures could be improved:

1) When discussing the decorrelation of neuronal responses by cholinergic axon activation, it is important to make it clear that Figure 6D quantifies the responses of layer 5 apical dendrites rather than neurons.

We have added this information to the results section.

2) In Figure S7, please clarify why velocity is in arbitrary units.

This was an oversight and has been fixed.

3) Please clarify how locomotion and stational trials are selected in Figure 4.

We thank the reviewers for pointing this out. Trials were classified as occurring during locomotion or while mice were stationary as follows. We used a time-window of -0.5 s to +1 s around stimulus onset. If mice exhibited uninterrupted locomotion above a threshold of 0.25 cm/s in this time-window, we considered the stimulus as occurring during locomotion, otherwise it was defined as occurring while the mice were stationary. Note, the same criteria to define locomotion state was used to isolate visuomotor mismatch events, and also during control optogenetic stimulation experiments. We have added this information to the methods.

4) When testing whether cholinergic activation is sufficient to explain locomotion-induced decorrelation in Figure 6G-H, please show pre-CNO and post-CNO delta-correlation, not just their difference.

We can do that, but the results are harder to parse this way. We have added this as Figure S11 to the manuscript. The problem with parsing the figure is that the pre-CNO levels are different in different groups. This is likely a function of mouse-to-mouse variability and makes it harder to identify what the CNO induced changes are. Using the pre-post difference removes the batch influence. Hence, we have left this as the main analysis in Figure 6G and 6H.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this study, Millard and colleagues investigated if the analgesic effect of nicotine on pain sensitivity, assessed with two pain models, is mediated by Peak Alpha Frequency (PAF) recorded with resting state EEG. The authors found indeed that nicotine (4 mg, gum) reduced pain ratings during phasic heat pain but not cuff pressor algometry compared to placebo conditions. Nicotine also increased PAF (globally). However, mediation analysis revealed that the reduction in pain ratings elicited by the phasic heat pain after taking nicotine was not mediated by the changes in PAF. Also, the authors only partially replicated the correlation between PAF and pain sensitivity at baseline (before nicotine treatment). At the group-level no correlation was found, but an exploratory analysis showed that the negative correlation (lower PAF, higher pain sensitivity) was present in males but not in females. The authors discuss the lack of correlation.

In general, the study is rigorous, methodology is sound and the paper is well-written. Results are compelling and sufficiently discussed.

Strengths:

Strengths of this study are the pre-registration, proper sample size calculation, and data analysis. But also the presence of the analgesic effect of nicotine and the change in PAF.

Weaknesses:

It would even be more convincing if they had manipulated PAF directly.

We thank Reviewer #1 for their positive and constructive comments regarding our study. We appreciate the view that the study was rigorous and methodologically sound, that the paper was well-written, and that the strengths included our pre-registration, sample size calculation, and data analysis.

In response to the reviewer's comment about more directly manipulating Peak Alpha Frequency (PAF), we agree that such an approach could provide a more direct investigation of the role of PAF in pain processing. We chose nicotine to modulate PAF as the literature suggested it was associated with a reliable increase in PAF speed. As mentioned in our Discussion, there are several alternative methods to manipulate PAF, such as non-invasive brain stimulation techniques (NIBS) like transcranial alternating current stimulation (tACS) or neurofeedback training. These approaches could help clarify whether a causal relationship exists between PAF and pain sensitivity. Although methods such as NIBS still require further investigation as there is little evidence for these approaches changing PAF (Millard et al., 2024).

Reviewer #2 (Public Review):

Summary:

The study by Millard et al. investigates the effect of nicotine on alpha peak frequency and pain in a very elaborate experimental design. According to the statistical analysis, the authors found a factor-corrected significant effect for prolonged heat pain but not for alpha peak frequency in response to the nicotine treatment.

Strengths:

I very much like the study design and that the authors followed their research line by aiming to provide a complete picture of the pain-related cortical impact of alpha peak frequency. This is very important work, even in the absence of any statistical significance. I also appreciate the preregistration of the study and the well-written and balanced introduction. However, it is important to give access to the preregistration beforehand.

Weaknesses:

The weakness of the study revolves around three aspects:

(1) I am not entirely convinced that the authors' analysis strategy provides a sufficient signal-tonoise ratio to estimate the peak alpha frequency in each participant reliably. A source separation (ICA or similar) would have been better suited than electrode ROIs to extract the alpha signal. By using a source separation approach, different sources of alpha (mu, occipital alpha, laterality) could be disentangled.

(2) Also, there's a hint in the literature (reference 49 in the manuscript) that the nicotine treatment may not work as intended. Instead, the authors' decision to use nicotine to modulate the peak alpha frequency and pain relied on other, not suitable work on chronic pain and permanent smokers. In the present study, the authors use nicotine treatment and transient painful stimulation on nonsmokers.

(3) In my view, the discussion could be more critical for some aspects and the authors speculate towards directions their findings can not provide any evidence. Speculations are indeed very important to generate new ideas but should be restricted to the context of the study (experimental pain, acute interventions). The unfortunate decision to use nicotine severely hampered the authors' aim of the study.

Impact:

The impact of the study could be to show what has not worked to answer the research questions of the authors. The authors claim that their approach could be used to define a biomarker of pain. This is highly desirable but requires refined methods and, in order to make the tool really applicable, more accurate approaches at subject level.

We thank reviewer #2 for their recognition of the study’s design, the importance of this research area, and the pre-registration of our study. In response to the weaknesses highlighted:

(1) We appreciate the reviewer’s suggestion to improve the signal-to-noise ratio by applying source separation techniques, such as ICA, which have now been performed and incorporated into the manuscript. Our original decision to use sensor-level ROIs followed the precedent set in previous studies, our rationale being to improve reproducibility and avoid  biases from picking individual electrodes or manually picking sources. We have  added analyses using an automated pipeline that selects components based on the presence of a peak in the alpha range and alignment with a predefined template topography representing sensorimotor sites. Here again we found no significant differences in the mediation results that used a sensor space sensorimotor ROI, further supporting the robustness of the chosen approach. ICA could still potentially disentangle different sources of alpha, such as occipital alpha and mu rhythm, and provide new insights into the PAF-pain relationship. We have now added a discussion in the manuscript about the potential advantages of source separation techniques and suggest that the possible contributions of separate alpha sources be investigated and compared to sensor space PAF as a direction for future research.

(2) We recognise the reviewer's concern regarding our choice of nicotine as a modulator of pain and alpha peak frequency (PAF). The meta-analysis by Ditre et al. (2016) indeed points to small effect sizes for nicotine's impact on experimental pain and highlights the potential for publication bias. However, our decision to use nicotine in this study was not primarily based on its direct analgesic effects, but rather on its well-documented ability to modulate PAF, in smoking and non-smoker populations, as outlined in our study aims.

In this regard, the intentional use of nicotine was to assess whether changes in PAF could mediate alterations in pain. This approach aligns with the broader concept that a direct effect of an intervention is not necessary to observe indirect effects (Fairchild & McDaniel, 2017). We have, however, revised our introduction to further clarify this rationale, highlighting that nicotine was used as a tool for PAF modulation, not solely for its potential analgesic properties.

(3) We agree with the reviewer’s observation that certain aspects of the Discussion could be more cautious, particularly regarding speculations about nicotine’s effects and PAF as a biomarker of pain. We have revised the Discussion to ensure that our interpretations are better grounded in the data from this study, clearly stating the limitations and avoiding overgeneralization. This revision focuses on a more critical evaluation of the potential relationships between PAF, nicotine, and pain sensitivity based solely on our experimental context.

Finally, We also apologize for not providing access to the preregistration earlier. This was an oversight on our end, and we will ensure that future preregistrations are made available upfront.

Reviewer #3 (Public Review):

In this manuscript, Millard et al. investigate the effects of nicotine on pain sensitivity and peak alpha frequency (PAF) in resting state EEG. To this end, they ran a pre-registered, randomized, double-blind, placebo-controlled experiment involving 62 healthy adults who received either 4 mg nicotine gum (n=29) or placebo (n=33). Prolonged heat and pressure were used as pain models. Resting state EEG and pain intensity (assessed with a visual analog scale) were measured before and after the intervention. Additionally, several covariates (sex at birth, depression and anxiety symptoms, stress, sleep quality, among others) were recorded. Data was analyzed using ANCOVAequivalent two-wave latent change score models, as well as repeated measures analysis of variance. Results do not show *experimentally relevant* changes of PAF or pain intensity scores for either of the prolonged pain models due to nicotine intake.

The main strengths of the manuscript are its solid conceptual framework and the thorough experimental design. The researchers make a good case in the introduction and discussion for the need to further investigate the association of PAF and pain sensitivity. Furthermore, they proceed to carefully describe every aspect of the experiment in great detail, which is excellent for reproducibility purposes. Finally, they analyse the data from almost every possible angle and provide an extensive report of their results.

The main weakness of the manuscript is the interpretation of these results. Even though some of the differences are statistically significant (e.g., global PAF, pain intensity ratings during heat pain), these differences are far from being experimentally or clinically relevant. The effect sizes observed are not sufficiently large to consider that pain sensitivity was modulated by the nicotine intake, which puts into question all the answers to the research questions posed in the study.

We would like to express our gratitude to Reviewer #3 for their thoughtful and constructive review, including the positive feedback on the strengths of our study's conceptual framework, experimental design, and thorough methodological descriptions.

We acknowledge the concern regarding the experimental and clinical relevance of some statistically significant results (e.g., global PAF and pain intensity during heat pain) and agree that small effect sizes may limit their practical implications. However, our primary goal was to assess whether nicotine-induced changes in PAF mediate pain changes, rather than to demonstrate large direct effects on pain sensitivity. Nicotine was chosen for its known ability to modulate PAF, and our focus was on the mechanistic role of PAF in pain perception. To clarify this, we have revised the discussion to better differentiate between statistical significance, experimental relevance, and clinical applicability. We emphasize that this study represents a preliminary step towards understanding PAF’s mechanistic role in pain, rather than a direct clinical application.

We appreciate the suggestion to refine our interpretation. We have adjusted our language to ensure it aligns with the effect sizes observed and made recommendations for future research, such as testing different nicotine doses, to potentially uncover stronger or more clinically relevant effects.

Although modest, we believe these findings offer valuable insights into the potential mechanisms by which nicotine affects alpha oscillations and pain. We have also discussed how these small effects could become more pronounced in different populations (e.g., chronic pain patients) and over time, offering guidance for future research on PAF modulation and pain sensitivity.

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

I have a number of points that the authors may want to consider for this or future work.

(1) By reviewing the literature provided by the authors in the introduction I think that using nicotine as a means to modulate pain and alpha peak frequency was a mistake. The only work that may give a hint on whether nicotine can modulate experimental pain is the meta-analysis by Ditre and colleagues (2016). They suggest that their small effect may contain a publication bias. I think the other "large body of evidence" is testing something else than analgesia.

Thank you for your consideration of our choice of nicotine in the study. The meta-analysis by Ditre and colleagues (2016) suggests small effect sizes for nicotine's impact on experimental pain, compared to the moderate effects claimed in some papers, especially when accounting for the potential publication bias you mentioned. However, our selection of nicotine was primarily driven by its documented ability to modulate PAF rather than its direct analgesic effects, as clearly stated in our aims. Therefore, we do not view our decision to use nicotine as a mistake; instead, it was aligned with our goal of assessing whether changes in PAF mediate alterations in pain and thus served as a valuable tool. This perspective aligns with the broader concept that a direct effect is not a prerequisite for observing indirect effects of an intervention on an outcome (Fairchild &

McDaniel, 2017). To further enhance clarity, we've revised the introduction to emphasize the role of nicotine in manipulating PAF in relation to our study's aims.

Previously we wrote: “A large body of evidence suggests that nicotine is an ideal choice for manipulating PAF, as both nicotine and smoking increase PAF speed [37,40–47] as well as pain thresholds and tolerance [48–52].” This has been changed to read: “Because evidence suggests that nicotine can modulate PAF, where both nicotine and smoking increase PAF speed [37,40–47], we chose nicotine to assess our aim of whether changes in PAF mediate changes in pain in a ‘mediation by design’ approach [48]. In addition, given evidence that nicotine may increase experimental pain thresholds and tolerance [49–53], nicotine could also influence pain ratings during tonic pain.”

(2) As mentioned above, the OSF page is not accessible.

We apologise for this. We had not realised that the pre-registration was under embargo, but we have now made it available.

(3) I generally struggle with the authors' approach to investigating alpha. With the approach the authors used to detect peak alpha frequency it might be that the alpha signal may just show such a low amplitude that it is impossible to reliably detect it at electrode level. In my view, the approach is not accurate enough, which can be seen by the "jagged" shape of the individual alpha peak frequency. In my view, a source separation technique would have been more useful. I wonder which of the known cortical alphas contributes to the effects the authors have reported previously: occipital, mu rhythms projections or something else? A source separation approach disentangles the different alphas and will increase the SNR. My suggestion would be to work on ICA components or similar approaches. The advantage is that the components are almost completely free of any artefacts. ICAs could be run on the entire data or separately for each individual. In the latter case, it might be that some participants do not exhibit any alpha component.

We appreciate your thoughtful consideration of our approach to investigating alpha. The calculation of PAF involves various methods and analysis steps across the literature (Corcoran et al., 2018; Gil Avila et al., 2023; McLain et al., 2022). Your query about which known cortical alphas contribute to reported effects is important. Initially focusing on a sensorimotor component from an ICA in Furman et al., 2018, subsequent work from our labs suggested a broader relationship between PAF and pain across the scalp (Furman et al., 2019; Furman et al., 2020; Millard et al., 2022), and a desire to conduct analyses at the sensor level in order to improve the reproducibility of the methods (Furman et al., 2020). However, based on your comment we have made several additions to the manuscript, including: explaining why we did not use manual ICA methods, suggest this for future research, and added an exploratory analysis using a recently developed automated pipeline that selects components based on the presence of a peak in the alpha range and alignment with a predefined template topography representing activity from occipital or motor sites.

While we acknowledge that ICA components can offer a better signal-to-noise ratio (SNR) and possibly smoother spectral plots, we opted for our chosen method to avoid potential bias inherent in deciding on a component following source separation. The desire for a quick, automated, replicable, and unbiased pipeline, crucial for potential clinical applications of PAF as a biomarker, influenced this decision. At the time of analysis registration, automated methods for deciding which alpha components to extract following ICA were not apparent. We have now added this reasoning to Methods.

“Contrary to some previous studies that used ICA to isolate sensory region alpha sources (Furman et al., 2018; De Martino et al., 2021; Valentini et al., 2022), we used pre-determined sensor level ROIs to improve reproducibility and reduce the potential for bias when individually selecting ICA components. Using sensor level ROIs may decrease the signal-to-noise ratio of the data; however, this approach has still been effective for observing the relationship between PAF and experimental pain (Furman et al., 2019; Furman et al., 2020).”

We have also added use of ICA and development of methods as a suggestion for future research in the discussion:

“Additionally, the use of global PAF may have introduced mediation measurement error into our mediation analysis. The spatial precision used in the current study was based on previous literature on PAF as a biomarker of pain sensitivity, which have used global and/or sensorimotor ROIs (Furman et al., 2018; Furman et al., 2020). Identification and use of the exploratory electrode clusters found in this study could build upon the current work (e.g., Furman et al., 2021). However, exploratory analysis of the clusters found in the present analysis demonstrated no influence on mediation analysis results (Supplementary Materials 3.8-3.10). Alternatively, independent component analysis (ICA) could be used to identify separate sources of alpha oscillations (Choi et al., 2005), as used in other experimental PAF-pain studies (Furman et al., 2018; Valentini et al., 2022), which could aid to disentangle the potential relevance of different alpha sources in the PAFpain relationship. Although this comes with the need to develop more reproducible and automated methods for identifying such components.”

The specific location or source of PAF that relates to pain remains unclear. Because of this, we did employ an exploratory cluster-based permutation analysis to assess the potential for variations in the presence of PAF changes across the scalp at sensor level, and emphasise that location of PAF change could be explored in future. However, we have now conducted the mediation analysis (difference score 2W-LCS model) using averages from the data-driven parietal cluster, frontal cluster, and both clusters together. For these we see a stronger effect of gum on PAF change, which was expected given the data driven approach of picking electrodes. There was still a total and direct effect of nicotine on pain during the PHP model, but still no indirect effect via change in PAF. For the CPA models, there were still no significant total, direct, or indirect effects of nicotine on CPA ratings. Therefore, using these data-driven clusters did not alter results compared to the model using the global PAF variable.

The reader has been directed to this supplementary material so:

“The potential mediating effect of this change in PAF on change in PHP and CPA was explored (not pre-registered) by averaging within each cluster (central-parietal: CP1, CP2, Cpz, P1, P2, P3, P4, Pz, POz; right-frontal: F8, FT8, FT10) and across both clusters. This averaging across electrodes produced three new variables, each assessed in relation to mediating effects on PHP and CPA ratings. The resulting in six exploratory mediation analysis (difference score 2W-LCS) models demonstrated minimal differences from the main analysis of global PAF (8-12 Hz), except for the

expected stronger effect of nicotine on change in PAF (bs = 0.11-0.14, ps < .003; Supplementary

Materials 3.8-3.10).”

Moreover, our team has been working on an automated method for selecting ICA components, so in response to your comment we assessed whether using this method altered the results of the current analysis. The in-depth methodology behind this new automatic pipeline will be published with a validation from some co-authors in the current collaboration in due course. At present, in summary, this automatic pipeline conducts independent component analysis (ICA) 10 times for each resting state, and selects the component with the highest topographical correlation to a template created of a sensorimotor alpha component from Furman et al., (2018). 

The results of the PHP or CPA mediation models were not substantially different using the PAF calculated from independent components than that using the global PAF. For the PHP model, the total effect (b = -0.648, p \= .033) and direct effects (b = -0.666, p \= .035) were still significant, and there was still no significant indirect effect (b = 0.018, p \= .726). The general fit was reduced, as although the CFI was above 0.90, akin to the original model, the RMSEA and SRMR were not below 0.08, unlike the original models (Little, 2013). For the CPA model, there were still no significant total (b = -0.371, p \= .357), direct (b = -0.364, p \= .386), or indirect effects (b = -0.007, p \= .906), and the model fit also decreased, with CFI below 0.90 and RMSEA and SRMR above 0.08. See supplementary material (3.11). Note that still no correlations were seen between this IC sensorimotor PAF and pain (PHP: r = 0.11, p = .4; CPA: r \= -0.064, p = .63).

Interestingly, in both models, there was now no longer a significant a-path (PHP: b = 0.08, p =

0.292; CPA: b = 0.039, p = 0.575), unlike previously observed (PHP: b = 0.085, p = 0.018; CPA: b = 0.089, p = 0.011). We interpret this as supporting the previously highlighted difference between finding an effect on PAF globally but not in a sensorimotor ROI (and now a sensorimotor IC), justifying the exploratory CBPA and the suggestion in the discussion to explore methodology.

We understand that this analysis does not fully uncover the reviewer’s question in which they wondered which of the known cortical alphas contributes to the effects reported in our previous work. However, we consider this exploration to be beyond the scope of the current paper, as it would be more appropriately addressed with larger datasets or combinations of datasets, potentially incorporating MEG to better disentangle oscillatory sources. The highlighted differences seen between global PAF, sensorimotor ROI PAF, sensorimotor IC PAF, as well as the CBPA of PAF changes provide ample directions for future research to build upon: 1) which alpha (sensor or source space) are related to pain, 2) how are these alpha signals represented robustly in a replicable way, and 3) which alpha (sensor or source space) are manipulable through interventions. These are all excellent questions for future studies to investigate.

The below text has been added to the Discussion:

In-house code was developed to compare a sensorimotor component to the results presented in this manuscript (Supplementary Material 3.11), showing similar results to the sensorimotor ROI mediation analysis presented here. However, examination of which alpha - be it sensor or source space - are related to pain, how they can be robustly represented, and how they can be manipulated are ripe avenues for future study.

(4) I have my doubts that you can get a reliable close to bell-shaped amplitude distribution for every participant. The argument that the peak detection procedure is hampered by the high-amplitude lower frequency can be easily solved by subtracting the "slope" before determining the peak. My issue is that the entire analysis is resting on the assumption that each participant has a reliable alpha effect at electrode level. This is not the case. Non-alpha participants can severely distort the statistics. ICA-based analyses would be more sensitive but not every participant will show alpha. You may want to argue with robust group effects but In my view, every single participant counts, particularly for this type of data analysis, where in the case of a low SNR the "peak" can easily shift to the extremes. In case there is an alpha effect for a specific subject, we should see a smooth bump in the frequency spectrum between 8 and 12 12Hz. Anything beyond that is hard to believe. The long stimulation period allows a broad FFT analysis window with a good frequency resolution in order to detect the alpha frequency bump.

The reviewer is correct that non-alpha participants can distort the statistics. We did visually assess the EEG of each individual’s spectra at baseline to establish the presence of global peaks, as we believe this is good practice to aid understanding of the data. Please see Author response image 1 for individual spectra seen at baseline. Although not all participants had a ‘smooth bump in the frequency spectrum between 8 and 12 Hz’, we prefer to not apply/necessitate this assumption to our data. Chiang et al., (2011) suggest that ~3% of individuals do not have a discernible alpha peak, and in our data we observed only one participant without a very obvious spectral peak (px-39). But, this participant does have enough activity within the alpha range to identify PAF by the CoG method (i.e. not just flat spectra and activity on top of 1/f characteristics). Without a pre-registered and standardised decision process to remove such a participant in place, we opted to not remove any participants to avoid curation of our data.

Author response image 1.

(5) I find reports on frequent channel rejections reflect badly on the data quality. Bad channels can be avoided with proper EEG preparation. EEG should be continuously monitored during recording in order to obtain best data quality. Have any of the ROI channels been rejected?

We appreciate your attention to the channel rejection. We believe that the average channels removed (0.94, 0.98, 0.74, and 0.87 [range: 0-4] for each of the four resting states out of 64 channels) does not suggest overly frequent rejection, as it was less than one electrode on average and the numbers are below the accepted number of bad channels to remove/interpolate (i.e. 10%) in EEG pipelines (Debnath et al., 2020; Kayhan et al., 2022). To maintain data quality, consistently poor channels were identified and replaced over time. We hope you will accept our transparency on this issue and note that by stating how channel removal decisions were made (i.e. 8 or more deviations) and reporting the number of channels removed, we adhere to the COBIDAS guidelines (Pernet et al., 2018; 2020).

During analysis, cases of sensorimotor ROI channels being rejected were noted and are now specified in our manuscript. “Out of 248 resting states recorded, 14 resting states had 4 ROI channels instead of 5. Importantly, no resting state had fewer than 4 channels for the sensorimotor ROI.”

Note, we also realised that we had not specified that we did interpolate channels for the cluster based permutation analysis. This has been corrected with the following sentence:

“Removed channels were not interpolated for the pre-registered global and sensorimotor ROI averaged analyses, but were interpolated for an exploratory cluster based permutation analysis using the nearest neighbour average method in `Fieldtrip`.”

(6) I have some issues buying the authors' claims that there is an effect of nicotine on prolonged pain. By looking at the mean results for the nicotine and placebo condition, this can not be right. What was the point in including the variables in the equation? In my view, in this within-subject design the effect of nicotine should be universal, no matter what gender, age, or depression. The unconditional effect of nicotine is close to zero. I can not get my head around how any of the variables can turn the effects into significance. There must be higher or lower variable scores that might be related to a higher or lower effect on nicotine. The question is not to consider these variables as a nuisance but to show how they modulate the pain-related effect of nicotine treatment. Still, the overall nicotine effect of the entire group is basically zero.

Another point is that for within-subject analyses even tiny effects can become statistically significant if they are systematically in one direction. This might be the case here. There might be a significant effect of nicotine on pain but the actual effect size (5.73 vs. 5.78) is actually not interpretable. I think it would be interesting for the reader how (in terms of pain rating difference) each of the variables can change the effect of nicotine.

Thank you for your comments. We recognize the concern about interpreting the effect of nicotine on prolonged pain solely based on mean results, and in fact wish to discourage this approach. It's crucial to note that both PAF and pain are highly individual measures (i.e. high inter-individual variance), necessitating the use of random intercepts for participants in our analyses to acknowledge the inherent variability at baseline across participants. Including random intercepts rather than only considering the means helps address the heterogeneity in baseline levels among participants. We also recognise that displaying the mean PHP ratings for all participants in Table 2 could be misleading, firstly because these means do not have weight in an analysis that takes into account a random-effects intercept for participants, and secondly because two participants (one from each group) did not have post-gum PHP assessments and were not included in the mediation analysis due to list-wise deletion of missing data. Therefore, to reduce the potential for misinterpretation, we have added extra detail to display both the full sample and CPA mediation analysis (i.e. N=62) and the data used for PHP mediation analysis (i.e. n=60) in Table 2. We hope that the extra details added to this table will help the readers interpretation of results.

In light of this, we have also altered the PAF Table 3 to reflect both the pre-post values used for the CPA mediation and baseline correlations with CPA and PHP pain (i.e. N=62), and the pre-post values used for the PHP mediation (i.e. n=60).

It is inherently difficult to visualise the findings of a mediation analysis with confounding variables that also used latent change scores (LCS) and random-effect intercepts for participants. LCS was specifically used because of issues of regression to the mean that occur if you calculate a straightforward ‘difference-score’, therefore calculating the difference in order to demonstrate the results of the statistical model in a figure, for example, does not provide a full description of the data assessed (Valente & McKinnon, 2017). Nevertheless, if we look at the data descriptively with this in mind, then calculating the change in PHP ratings does indicate that, for the nicotine group, the mean change in PHP ratings was -0.047 (SD = 1.05, range: -4.13, 1.45). Meanwhile, for the placebo group the mean change in PHP ratings was 0.33 (SD = 0.75, range: -1.37, 1.66). Therefore suggesting a slight decrease in pain ratings on average for the nicotine group compared to a slight increase on average for the placebo group. With control for pre-determined confounders, we found that the latent change score was -0.63 lower for the nicotine group compared to the control group (i.e. the direct effect of nicotine on change in pain).

If the reviewer is only discussing the effect of nicotine on pain, we do not believe that this effect ‘should be universal’. There is clear evidence that effects of nicotine on other measures can vary greatly across individuals (Ettinger et al., 2009; Falco & Bevins, 2015; Pomerleau et al., 1995). Our intention would not be to propose a universal effect but to understand how these variables may influence nicotine's impact on pain for individuals. Here we focus on the effects of nicotine on PAF and pain sensitivity, but attempted to control for the potential influence of these other confounding factors. Therefore, our statistical approach goes beyond mean values, incorporating variables like sex at birth, age, and depression to control for and explore potential modulating factors. Control for confounding factors is an important aspect of mediation analysis (Lederer et al., 2019; VanderWeele, 2019).

Regarding the seemingly small effect size, we understand your concern. Indeed ‘tiny effects can become statistically significant if they are systematically in one direction’, which may be what we see in this analysis. We do not agree that the effect is ‘not interpretable’, rather that it should be interpreted in light of its small effect size (effect size being the beta coefficient in our analysis, rather than the mean group difference). We agree on the importance of considering practical significance alongside statistical significance and hope to conduct additional experiments and analyses in future to elucidate the contribution of each variable to the subtle and therefore not entirely conclusive overall effect you mention.

Your feedback on this is valuable, and we have ensured a more detailed discussion in the revised manuscript on how these factors should be interpreted alongside some additional post-hoc analyses of confounding factors that were significant in our mediation, with the note that investigation of these interactions is exploratory. We had already discussed the potential contribution of sex on the effect of nicotine on PAF, with exploratory post-hoc analysis on this included in supplementary materials. In addition, we have now added an exploratory post-hoc analysis on the potential contribution of stress on the effect of nicotine on pain. This then shows the stratified effects by the covariates that our model suggest are influencing change in PAF and pain.

Results edits:

“There was also a significant effect of perceived stress at baseline on change in PHP ratings when controlling for group allocation and other confounding variables (b = -0.096, p = .048, bootstrapped 95% CI: [-0.19, -0.000047]), where higher perceived stress resulted in larger decreases in PHP ratings (see Supplementary Material 3.3 for post-hoc analysis of stress).”

Supplementary material addition:

“3.3 Exploratory analysis of the influence of perceived stress on the effects of nicotine on change in PHP ratings “

“Due to the significant estimated effects of perceived stress on change in PHP ratings in the 2WLCS mediation model, we also explored post-hoc effects of stress on change in PHP ratings. We found that there is strong evidence for a negative correlation between stress and change in PHP rating within the nicotine group (n = 28, r = −0.39, BF10 = 13.65; Figure 3) that is not present in the placebo group, with equivocal evidence (n = 32, r = −0.14, BF10 = 0.46). This suggests that those with higher baseline stress who had nicotine gum experienced greater decreases in PHP ratings. Note that there was less, but still sufficient evidence for this relationship within the nicotine group when the participant who was a potential outlier for change in PHP rating was removed (n = 27, r = −0.32, BF10 = 1.45). “

Author response image 2.

Spearman correlations od baseline perceived stress with the change in phasic heat pain (PHP) ratings, suggest strong evidence for a negative relationship for the nicotine gum groupin orange (n=28; BF₁₀=13.65) but not for the placebo group in grey (n=32; BF₁₀=0.46). Regression lines and 95% confidence intervals.

Discussion edits:

“For example, in addition to the effect of nicotine on prolonged heat pain ratings, our results suggest an effect of stress on changes in heat pain ratings, with those self-reporting higher stress at baseline having greater reductions in pain. Our post-hoc analysis suggested that this relationship between higher stress and larger decrease in PHP ratings was only present for the nicotine group (Supplementary Material 3.3). As stress is linked to nicotine use [69,70] and pain [71–73], these interactions should be explored in future.”

(7) Is the differential effect of nicotine vs. placebo based on the pre vs. post treatment effect of the placebo condition or on the pre vs. post effect of the nicotine treatment? Can the mediation model be adapted and run for each condition separately? The placebo condition seems to have a stronger effect and may have driven the result.

Thank you for your comments. In our mediation analysis, the differential effect of nicotine vs. placebo is assessed as a comparison between the pre-post difference within each condition. A latent change score (i.e. pre-post) is calculated for each condition (nicotine and placebo), and then the effect of being in the nicotine group (dummy coded as 1) is compared to being in the placebo group (dummy coded as 0). The comparison between conditions is needed for this model (Valente & MacKinnon, 2017), as we are assessing the change in PAF and pain in the nicotine group compared to the change in the placebo group.

However, to address your response, it is possible to simplify and assess the relationship between the change in peak alpha frequency (PAF) and change in pain within each gum group (nicotine and placebo) independently, without including the intervention as a factor. To do this, the mediation model can be simplified to regression analysis with latent change scores that focus purely on these relationships. The results of this can help to understand whether change in PAF influences change in pain within each group separately. As with the main analysis, we see no significant influence of change in PAF on change in pain while controlling for the same confounding variables within the nicotine group (Beta = -0.146 +/- 1.105, p = 0.895, 95% CI: -2.243, 2.429) or the placebo group (Beta = 0.730 +/- 2.061, p = 0.723, 95% CI: -4.177, 3.625).

When suggesting that the “the placebo condition seems to have a stronger effect and may have driven the result”, we believe you are referring to the increase in mean PHP ratings within the placebo group from pre (5.51 +/- 2.53) to post-placebo gum (5.84 +/- 2.67). Indeed there was a significant increase in pain ratings pre to post chewing placebo gum (t(31) = -2.53, p = 0.0165, 95% CI: -0.603, -0.0653), that was not seen after chewing nicotine gum (t(27) = 0.237, p = 0.81, 95% CI: -0.358, 0.452). In lieu of a control where no gum was chewed (i.e. simply a second pain assessment ~30 minutes after the first), we assume the gum without nicotine is a good reference that controls for the effect of time plus expectation of chewing nicotine gum. With this in mind, as we describe in our results, the change in PHP ratings is reduced in the nicotine group compared to the placebo group. Note that this phrasing keeps the effect of placebo on pain as our reference from which to view the effect of nicotine on pain. However, you are correct that we need to ensure we emphasise that the change in pain in the PHP group is reduced in comparison to the change seen after placebo.

We have not included these extra statistics in our revised manuscript, but hope that they aid the your understanding and interpretation of the included analyses and have highlighted these nuances in the discussion.

“However, we note that the observed effect of nicotine on pain was small in magnitude, and most prominent in comparison to the effect of placebo, where pain ratings increased after chewing, which brings into question whether this reduction in pain is meaningful in practice.”

(8) I would not dare to state that nicotine can function as an acute analgesic. Acute analgesics need to work for everyone. The average effect here is close to zero.

In light of your feedback, we have refined our language to avoid a sweeping assertion of universal analgesic effects and emphasize individual variability. Nicotine's role as a coping strategy for pain is acknowledged in the literature (Robinson et al., 2022), with the meta-analysis by Ditre et al. (2016) discussing its potential as an acute analgesic in humans, along with some evidence from animal research (Zhang et al., 2020). Our revised discussion underscores the need for further exploration into factors influencing nicotine's potential impact on pain. We have also specified the short-term nature of nicotine use in this context to distinguish acute effects from potential opposing effects after long-term use (Zhang et al., 2020).

“Short-term nicotine use is thought to have acute analgesic properties in experimental settings, with a review reporting that nicotine increased pain thresholds and pain tolerance [49]. In addition, research in a rat model suggests analgesic effects on mechanical thresholds after short-term nicotine use (Zhang et al., 2020). However, previous research has not assessed the acute effects of nicotine on prolonged experimental pain models. The present study found that 4 mg of nicotine reduced heat pain ratings during prolonged heat pain compared to placebo for our human participants, but that prolonged pressure pain decreased irrespective of which gum was chewed. Our findings are thus partly consistent with the idea that nicotine may have acute analgesic properties [49], although further research is required to explore factors that may influence nicotine’s potential impact on a variety of prolonged pain models. We further advance the literature by reporting this effect in a

model of prolonged heat pain, which better approximates the experience of clinical pain than short lasting models used to assess thresholds and tolerance [50]. However, we note that the observed effect of nicotine on pain was small in magnitude, and most prominent in comparison to the effect of placebo, where pain ratings increased after chewing, which brings into question whether this reduction in pain is meaningful in practice. Future research should examine whether effects on pain increase in magnitude with different nicotine administration regimens (i.e. dose and frequency).”

(9) Figures 2E and 2F are not particularly intuitive. Usually, the colour green in "jet" colour coding is being used for "zero" values. I would suggest to cut off the blue and use only the range between red green and red.

We have chosen to retain the current colour scale for several reasons. In our analysis, green represents the middle of the frequency range (approx 10 Hz in this case), and if we were to use green as zero, it would effectively remove both blue and green from the plot, resulting in only red shades. Additionally, we have provided a clear colour scale for reference next to the plot, which allows readers to interpret the data accurately. Our intention is to maintain clarity and precision in representing the data, rather than conforming strictly to conventional practices in color coding.

We believe that the current representation effectively conveys the results of our study while allowing readers to interpret the data within the context provided. Thank you again for your suggestion, and we hope you understand our reasoning in this matter.

(10) Did the authors do their analysis on the parietal ROI or on the pre-registerred ROI?

The analysis was conducted on the pre-registered sensorimotor ROI and on the global values. We have now also conducted the analysis with the regions suggested with the cluster based permutation analysis as requested by reviewer 2, comment 3.

(11) Point 3.2 in the discussion. I would be very cautious to discuss smoking and chronic pain in the context of the manuscript. The authors can not provide any additional knowledge with their design targeting non-smokers, acute nicotine and experimental pain. The information might be interesting in the introduction in order to provide the reader with some context but is probably misleading in the discussion.

We appreciate your perspective and agree with your caution regarding the discussion of smoking and chronic pain. While our study specifically targets non-smokers and focuses on acute nicotine effects in experimental pain, we understand the importance of contextual clarity. We have removed these points from the discussion to not mislead the reader.

Previously we wrote, and have removed: “For those with chronic pain, smoking and nicotine use is reported as a coping strategy for pain [52]; abstinence can increase pain sensitivity [48,50], and pain is thus seen as a barrier to smoking cessation due to fear of worsening pain [51,52]. Therefore, continued understanding of the acute effects of nicotine on models of prolonged pain could improve understanding of the role of nicotine and smoking use in chronic pain [49,51,52].”

(12) I very much appreciate section 3.3 of the discussion. I would not give up on PAF as a target to modulate pain. A modulation might not be possible in such a short period of experimental intervention. PAF might need longer and different interventions to gradually shift in order to attenuate the intensity of pain. As discussed by the authors themselves, I would also consider other targets for alpha analysis (as mentioned above not other electrodes or ROIs but separated sources.)

Thank you for your comments on section 3.3. We appreciate your recognition of the potential significance of PAF as a target for pain modulation. Your insights align with our considerations that the experimental intervention duration or type might be a limiting factor in observing substantial shifts in PAF to attenuate pain intensity. We had mentioned the use of the exploratory electrode clusters in future work, but have now also mentioned that the use of ICA to identify separate ICA sources may provide an alternative approach. See responses to your previous ICA comment regarding separate sources.

REFERENCES for responses to reviewer 2

Chiang, A. K. I., Rennie, C. J., Robinson, P. A., Van Albada, S. J., & Kerr, C. C. (2011). Age trends and sex differences of alpha rhythms including split alpha peaks. Clinical Neurophysiology, 122(8), 1505-1517.

Debnath, R., Buzzell, G. A., Morales, S., Bowers, M. E., Leach, S. C., & Fox, N. A. (2020). The Maryland analysis of developmental EEG (MADE) pipeline. Psychophysiology, 57(6), e13580.

Ettinger, U., Williams, S. C., Patel, D., Michel, T. M., Nwaigwe, A., Caceres, A., ... & Kumari, V. (2009). Effects of acute nicotine on brain function in healthy smokers and non-smokers: estimation of inter-individual response heterogeneity. Neuroimage, 45(2), 549-561.

Falco, A. M., & Bevins, R. A. (2015). Individual differences in the behavioral effects of nicotine: a review of the preclinical animal literature. Pharmacology Biochemistry and Behavior, 138, 80-90.

Kayhan, E., Matthes, D., Haresign, I. M., Bánki, A., Michel, C., Langeloh, M., ... & Hoehl, S. (2022). DEEP: A dual EEG pipeline for developmental hyperscanning studies. Developmental cognitive neuroscience, 54, 101104.

Lederer, D. J., Bell, S. C., Branson, R. D., Chalmers, J. D., Marshall, R., Maslove, D. M., ... & Vincent, J. L. (2019). Control of confounding and reporting of results in causal inference studies. Guidance for authors from editors of respiratory, sleep, and critical care journals. Annals of the American Thoracic Society, 16(1), 22-28.

Little TD. Longitudinal structural equation modeling. Guilford press; 2013.

Pernet, C., Garrido, M., Gramfort, A., Maurits, N., Michel, C. M., Pang, E., ... & Puce, A. (2018). Best practices in data analysis and sharing in neuroimaging using MEEG.

Pernet, C., Garrido, M. I., Gramfort, A., Maurits, N., Michel, C. M., Pang, E., ... & Puce, A. (2020). Issues and recommendations from the OHBM COBIDAS MEEG committee for reproducible EEG and MEG research. Nature neuroscience, 23(12), 1473-1483.

Pomerleau, O. F. (1995). Individual differences in sensitivity to nicotine: implications for genetic research on nicotine dependence. Behavior genetics, 25(2), 161-177.

Robinson, C. L., Kim, R. S., Li, M., Ruan, Q. Z., Surapaneni, S., Jones, M., ... & Southerland, W. (2022). The Impact of Smoking on the Development and Severity of Chronic Pain. Current Pain and Headache Reports, 26(8), 575-581.

Xia, J., Mazaheri, A., Segaert, K., Salmon, D. P., Harvey, D., Shapiro, K., ... & Olichney, J. M. (2020). Event-related potential and EEG oscillatory predictors of verbal memory in mild cognitive impairment. Brain communications, 2(2), fcaa213.

VanderWeele, T. J. (2019). Principles of confounder selection. European journal of epidemiology, 34, 211-219.

Valente, M. J., & MacKinnon, D. P. (2017). Comparing models of change to estimate the mediated effect in the pretest–posttest control group design. Structural Equation Modeling: A Multidisciplinary Journal, 24(3), 428-450.

Vimolratana, O., Aneksan, B., Siripornpanich, V., Hiengkaew, V., Prathum, T., Jeungprasopsuk, W., ... & Klomjai, W. (2024). Effects of anodal tDCS on resting state eeg power and motor function in acute stroke: a randomized controlled trial. Journal of NeuroEngineering and Rehabilitation, 21(1), 1-15.

Zhang, Y., Yang, J., Sevilla, A., Weller, R., Wu, J., Su, C., ... & Candiotti, K. A. (2020). The mechanism of chronic nicotine exposure and nicotine withdrawal on pain perception in an animal model. Neuroscience letters, 715, 134627.

Reviewer #3 (Recommendations For The Authors):

Introduction

(1) Rationale and link to chronic pain. I am not sure I agree with the statement "The ability to identify those at greater risk of developing chronic pain is limited". I believe there is an abundance of literature associating risk factors with the different instances of chronic pain (e.g., Mills et al., 2019). The fact that the authors cite studies involving potential neuroimaging biomarkers leads me to believe that they perhaps did not intend to make such a broad statement, or that they wanted to focus on individual prediction instead of population risk.

We thank the reviewer for the thought put into this comment. We did indeed wish to refer to individual prediction, but also realise that the focus on predicting pain might not be the most appropriate opening for this manuscript. Therefore, we have adjusted the below sentence to refer to the need to identify modifiable factors rather than the need to predict pain.

“Identifying modifiable factors that influence pain sensitivity could be a key step in reducing the presence and burden of chronic pain (van der Miesen et al., 2019; Davis et al., 2020; Tracey et al., 2021).”

(2) The statement "Individual peak alpha frequency (PAF) is an electro-physiological brain measure that shows promise as a biomarker of pain sensitivity, and thus may prove useful for predicting chronic pain development" is a non sequitur. PAF may very well be a biomarker of pain sensitivity, but the best measures of pain sensitivity we have (selfreported pain intensity ratings) in general are not in themselves predictive of the development of chronic pain. Conversely, features that are not related to pain sensitivity could be useful for predicting chronic pain (e.g., Tanguay-Sabourin et al., 2023).

We agree that it is essential to acknowledge that self-reported pain intensity ratings alone are not definitive predictors of chronic pain development. To align with this, we have revised the sentence, removing the second clause to avoid overstatement. The adjusted sentence now reads, "Individual peak alpha frequency (PAF) is an electrophysiological brain measure that shows promise as a biomarker of pain sensitivity."

(3) Finally, some of the statements in the discussion comparing a tonic heat pain model with chronic neuropathic pain might be an overstatement. Whereas it is true that some of the descriptors are similar, the time courses and mechanisms are vastly different.

We appreciate this comment, and agree that it is difficult to compare the heat pain model used to clinical neuropathic pain. This was an oversight and with further understanding we have removed this comment from the introduction and the discussion:

“In parallel, we saw no indication of a relationship between PAF and pain ratings during CPA. The introduction of the CPA model, specifically calibrated to a moderate pain threshold, provides further support for the notion that the relationship between PAF and pain is specific to certain pain types [17,28]. Prolonged heat pain was pre-dominantly described as moderate/severe shooting, sharp, and hot pain, whereas prolonged pressure pain was predominantly described as mild/moderate throbbing, cramping, and aching in the present study. It is possible that the PAF–pain relationship is specific to particular pain models and protocols [12,17].”

Methodology

(4) or the benefit of good science. However, I am compelled to highlight that I could not access the preregistered files, even though I waited for almost two weeks after requesting permission to do so. This was a problem on two levels: the main one is that I could not check the hypothesized effect sizes of the sample size estimation, which are not only central to my review, and in general negate all the benefits that should go with preregistration (i.e., avoiding phacking, publication bias, data dredging, HARKing, etc.). The second one is that I had to provide an email address to request access. This allows the authors to potentially identify the reviewers. Whereas I have no issues with this and I support transparent peer review practices (https://elifesciences.org/inside-elife/e3e90410/increasingtransparency-in-elife-s-review-process), I also note that this might condition other reviewers.

We apologise for this. We had not realised that the pre-registration was under embargo, but we have now made it available.

Interpretation of results

(5)To be perfectly clear, I trust the results of this study more than some of the cited studies regarding nicotine and pain because it was preregistered, the sample size is considerably larger, and it seems carefully controlled. I just do not agree with the interpretation of the results, stated in the first paragraph of the Discussion. Quoting J. Cohen, "The primary product of a research inquiry is one or more measures of effect size, not P values" (Cohen, 1990). As I am sure the authors are aware of, even tiny differences between conditions, treatments or groups will eventually be statistically significant given arbitrarily large sample sizes. What really matters then is the magnitude of these differences. In general, the authors hypothesize on why there were no differences on the pressure pain model, and why decreases in heat pain were not mediated by PAF, but do not seem to consider the possibility that the intervention just did not cause the intended effect on the nociceptive system, which would be a much more straightforward explanations for all observations.

While acknowledging and agreeing with the concern that 'even tiny differences between conditions, treatments, or groups will eventually be statistically significant given arbitrarily large sample sizes,' it's crucial to clarify that our sample size of N=62 does not fall into the category of arbitrarily large. We carefully considered the observed outcomes in the pressure pain model and the lack of PAF mediation in heat pain, as dictated by our statistical approach and the obtained results.

The suggestion of a straightforward explanation aligning with the intervention not causing the intended effect on the nociceptive system is a valid consideration. We did contemplate the possibility of a false positive, emphasising this in the limitations of our findings and the need for replication to draw stronger conclusions to follow up this initial study.

(6) In this regard, I do not believe that an average *increase* of 0.05 / 10 (Nicotine post - pre) can be considered a "reduction of pain ratings", regardless of the contrast with placebo (average increase of 0.24 / 10). This tiny effect size is more relevant in the context of the considerable inter-individual variation, in which subjects scored the same heat pain model anywhere from 1 to 10, and the same pressure pain model anywhere from 1 to 8.5. In this regard, the minimum clinically or experimentally important differences (MID) in pain ratings varies from study to study and across painful conditions but is rarely below 1 / 10 in a VAS or NRS scale, see f. ex. (Olsen et al., 2017). It is not my intention to question whether nicotine can function as an acute analgesic in general (as stated in the Discussion), but instead, if it worked as such under these very specific experimental conditions. I also acknowledge that the authors note this issue in two lines in the Discussion, but I believe that this is not weighed properly.

We appreciate your perspective on the interpretation of the effect size, and we understand the importance of considering it in the context of individual variation.

As also discussed in response to comment 6 From reviewer 2, we recognize the concern about interpreting the effect of nicotine on prolonged pain solely based on mean results, and in fact wish to discourage this approach. It's crucial to note that both PAF and pain are highly individual measures (i.e. high inter-individual variance), necessitating the use of random intercepts for participants in our analyses to acknowledge the inherent variability at baseline across participants. Including random intercepts rather than only considering the means helps address the heterogeneity in baseline levels among participants. We also recognise that displaying the mean PHP ratings for all participants in Table 2 could be misleading, firstly because these means do not have weight in an analysis that takes into account a random-effects intercept for participants, and secondly because two participants (one from each group) did not have post-gum PHP assessments and were not included in the mediation analysis due to list-wise deletion of missing data. Therefore, to reduce the potential for misinterpretation, we have added extra detail to display both the full sample and CPA mediation analysis (i.e. N=62) and the data used for PHP mediation analysis (i.e. n=60) in Table 2. We hope that the extra details added to this table will help the readers interpretation of results.

Moreover, we have made sure refer to the comparison with the placebo group when discussing the reduction or decrease in pain seen in the nicotine group, for example:

“2) nicotine reduced prolonged heat pain intensity but not prolonged pressure pain intensity compared to placebo gum;”

“The nicotine group had a decrease in heat pain ratings compared to the placebo group and increased PAF speed across the scalp from pre to post-gum, driven by changes at central-parietal and right-frontal regions.”

We have kept our original comment of whether this effect on pain is meaningful in practice to refer to the minimum clinically or experimentally important differences in pain ratings as highlighted by Olsen et al., 2017.

“While acknowledging the modest effect size, it’s essential to consider the broader context of our study’s focus. Assessing the clinical relevance of pain reduction is pertinent in applications involving the use of any intervention for pain management [69]. However, from a mechanistic standpoint, particularly in understanding the implications of and relation to PAF, the specific magnitude of the pain effect becomes less pivotal. Nevertheless, future research should examine whether effects on pain increase in magnitude with different nicotine administration regimens (i.e. dose and frequency).”

(7) In line with the topic of effect sizes, average effect sizes for PAF in the study cited in the manuscript range from around 1 Hz (Boord et al., 2008; Wydenkeller et al., 2009; Lim et al., 2016), to 2 Hz (Foulds et al., 1994), compared with changes of 0.06 Hz (Nicotine post - pre) or -0.01 Hz (Placebo post - pre). MIDs are not so clearly established for peak frequencies in EEG bands, but they should be certainly larger than some fractions of a Hertz (which is considerably below the reliability of the measurement).

We appreciate your care of these nuances. We acknowledge the differences in effect sizes between our study and those referenced in the manuscript. Given the current state of the literature, it's noteworthy that ‘MIDs’ for peak frequencies in EEG bands, particularly PAF changes, are not clearly established, other than a recent publication suggesting that even small changes in PAF are reliable and meaningful (Furman et al., 2021). In light of this, we have addressed the uncertainty around the existence and determination of MIDs in our revision, highlighting the need for further research in this area.

In addition, our study employed a greater frequency resolution (0.2 Hz) compared to some of the referenced studies, with approximately 0.5 Hz resolution (Boord et al., 2008; Wydenkeller et al., 2009; Foulds et al., 1994). This improved resolution allows for a more precise measurement of changes in PAF. Considering this, it is plausible that studies with lower resolution might have conflated increases in PAF, and our higher resolution contributes to a more accurate representation of the observed changes.

We have also incorporated this insight into the manuscript, emphasising the methodological advancements in our study and their potential impact on the interpretation of PAF changes. Thank you for your thoughtful feedback.

“The ability to detect changes in PAF can be considerably impacted by the frequency resolution used during Fourier Transformations, an element that is overlooked in recent methodological studies on PAF calculation [16,95]. Changes in PAF within individuals might be obscured or conflated by lower frequency resolutions, which should be considered further in future research.”

(8) The authors also ran alternative statistical models to analyze the data and did not find consistent results in terms of PHP ratings (PAF modulation was still statistically significantly different). The authors attribute this to the necessity of controlling for covariates. Now, considering the effects sizes, aren't these statistically significant differences just artifacts stemming from the inclusion of too many covariates (Simmons et al., 2011)? How much influence should be attributable to depression and anxiety symptoms, stress, sleep quality and past pain, considering that these are healthy volunteers? Should these contrasting differences call the authors to question the robustness of the findings (i.e., whether the same data subjected to different analysis provides the same results), particularly when the results do not align with the preregistered hypothesis (PAF modulation should occur on sensorimotor ROIs)?

Thank you for your comments on our alternative statistical models. By including these covariates, we aim to provide a more nuanced understanding of the complexities within our data by considering their potential impact on the effects of interest. The decision to include covariates was preregistered (apologies again that this was not available) and made with consideration of balancing model complexity and avoiding potential confounding. Moreover, we hope that the insights gained from these analyses will offer valuable information about the behaviour of our data and aid future research in terms of power calculations, expected variance, and study design.

(9) Beyond that, I believe in some cases that the authors overreach in an attempt to provide explanations for their results. While I agree that sex might be a relevant covariate, I cannot say whether the authors are confirming a pre-registered hypothesis regarding the gender-specific correlation of PAF and pain, or if this is just a post hoc subgroup analysis. Given the large number of analyses performed (considering the main document and the supplementary files), caution should be exercised on the selective interpretation of those that align with the researchers' hypotheses.

We chose to explore the influence of sex on the correlation between PAF and pain, because this has also been investigated in previous publications of the relationship (Furman et al., 2020).  We state that the assessment by sex is exploratory in our results on p.17: “in an exploratory analysis of separate correlations in males and females (Figure 5, plot C)”. For clarity regarding whether this was a pre-registered exploration or not, we have adjusted this to be: “in an exploratory analysis (not pre-registered) of separate correlations in males and females (Figure 5, plot C), akin to those conducted in previous research on this topic (Furman et al., 2020),

We have made sure to state this in the discussion also. Therefore, when we previously said on p.22:

“Regarding the relationship between PAF and pain at baseline, the negative correlation between PAF and pain seen in previous work [7–11,15] was only observed here for male participants during the PHP model for global PAF.” We have now changed this to: “Regarding the relationship between PAF and pain at baseline, the negative correlation between PAF and pain seen in previous work [7– 11,15] was only observed here for male participants during the PHP model for global PAF in an exploratory analysis.”

Please also note that we altered the colour and shape of points on the correlation plot (Figure 5 in initial submission), the male brown was changed to a dark brown as we realised that the light brown colour was difficult to read. The shape was then changed for male points so that the two groups can be distinguished in grey-scale.

Overall, your thoughtful feedback is instrumental in refining the interpretation of our findings, and we look forward to presenting a more comprehensive and nuanced discussion. Thank you for your comments.

REFERENCES for responses to reviewer 3

Arendt-Nielsen, L., & Yarnitsky, D. (2009). Experimental and clinical applications of quantitative sensory testing applied to skin, muscles and viscera. The Journal of Pain, 10(6), 556-572.

Chowdhury, N. S., Skippen, P., Si, E., Chiang, A. K., Millard, S. K., Furman, A. J., ... & Seminowicz, D. A. (2023). The reliability of two prospective cortical biomarkers for pain: EEG peak alpha frequency and TMS corticomotor excitability. Journal of Neuroscience Methods, 385, 109766.

Fishbain, D. A., Lewis, J. E., & Gao, J. (2013). Is There Significant Correlation between SelfReported Low Back Pain Visual Analogue Scores and Low Back Pain Scores Determined by Pressure Pain Induction Matching?. Pain practice, 13(5), 358-363.

Furman, A. J., Prokhorenko, M., Keaser, M. L., Zhang, J., Chen, S., Mazaheri, A., & Seminowicz, D. A. (2021). Prolonged pain reliably slows peak alpha frequency by reducing fast alpha power.

bioRxiv, 2021-07.

Heitmann, H., Ávila, C. G., Nickel, M. M., Dinh, S. T., May, E. S., Tiemann, L., ... & Ploner, M. (2022). Longitudinal resting-state electroencephalography in patients with chronic pain undergoing interdisciplinary multimodal pain therapy. Pain, 163(9), e997.

McLain, N. J., Yani, M. S., & Kutch, J. J. (2022). Analytic consistency and neural correlates of peak alpha frequency in the study of pain. Journal of neuroscience methods, 368, 109460.

Ngernyam, N., Jensen, M. P., Arayawichanon, P., Auvichayapat, N., Tiamkao, S., Janjarasjitt, S., ... & Auvichayapat, P. (2015). The effects of transcranial direct current stimulation in patients with neuropathic pain from spinal cord injury. Clinical Neurophysiology, 126(2), 382-390.

Parker, T., Huang, Y., Raghu, A. L., FitzGerald, J., Aziz, T. Z., & Green, A. L. (2021). Supraspinal effects of dorsal root ganglion stimulation in chronic pain patients. Neuromodulation: Technology at the Neural Interface, 24(4), 646-654.

Petersen-Felix, S., & Arendt-Nielsen, L. (2002). From pain research to pain treatment: the role of human experimental pain models. Best Practice & Research Clinical Anaesthesiology, 16(4), 667680.

Sarnthein, J., Stern, J., Aufenberg, C., Rousson, V., & Jeanmonod, D. (2006). Increased EEG power and slowed dominant frequency in patients with neurogenic pain. Brain, 129(1), 55-64.

Sato, G., Osumi, M., & Morioka, S. (2017). Effects of wheelchair propulsion on neuropathic pain and resting electroencephalography after spinal cord injury. Journal of Rehabilitation Medicine, 49(2), 136-143.

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Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

Amaral et al. presents a study investigating the mesoscale modelling and dynamics of bolalipids.

Strengths:

The figures in this paper are exceptional. Both those to outline and introduce the lipid types, but also the quality and resolution of the plots. The data held within also appears to be outstanding and of significant (hopefully) general interest.

We thank the reviewer for their kind words and the appreciation of our work.

Weaknesses:

In the introduction, I would like to have read more specifics on the biological role of bolalipids. Archaea are mentioned, but this kingdom is huge - there must be specific species that can be discussed where bolalipids are integral to archaeal life. The authors should go beyond ’extremophiles’. In short, they should unpack why the general audience should be interested in these lipids, within a subset of organisms that are often forgotten about.

Following the reviewer’s advice we have revised the introduction of the manuscript, in which we now discuss specific species (Sulfolobus acidocaldarius and Thermococcus kodakarensis) and how in these species bolalipids are integral to archaeal life. We explain that the ratio between bilayer and bolalipids, and the number of cyclopentane rings contained within bolalipids can change to adapt to the environment. The revised parts of the introduction read (p.1 ):

“Like for bacteria and eukaryotes, archaea must keep their lipid membranes in a fluid state (homeoviscous adaptation). This is important even under extreme environmental conditions, such as hot and cold temperatures, or high and low pH values [7]. Because of this, many archaea adapt to changes in their environment by tuning the lipid composition of their membranes: altering the ratio between bola- and bilayer lipids in their membranes [8, 9] and/or by changing the number of cyclopentane rings in their lipid tails, which are believed to make lipid molecules more rigid [5]. For example, Thermococcus kodakarensis increases its tetraether bolalipid ratio from around 50% to over 80% when the temperature of the environment increases from 60 to 85 C [10]. Along the same lines, the cell membrane of Sulfolobus acidocaldarius, can contain over 90 % of bolalipids with up to 8 cyclopentane rings at 70 C and pH 2.5 [5, 11]. It is worth mentioning that in exceptional cases bacteria also synthesise bolalipids in response to high temperatures [12], highlighting that the study of bolalipid membranes is relevant not only for archaeal biology but also from a general membrane biophysics perspective.”

Reviewer #2 (Public review):

Summary:

The authors aimed to understand the biophysical properties of archeal membranes made of bolalipids. Bacterial and eukaryotic membranes are made of lipids that self-assemble into bilayers. Archea, instead, use bolalipids, lipids that have two headgroups and can span the entire bilayer. The authors wanted to determine if the unique characteristics of archaea, which are often extremophiles, are in part due to the fact that their membranes contain bolalipids.

The authors develop a minimal computational model to compare the biophysics of bilayers made of lipids, bolalipids, and mixtures of the two. Their model enables them to determine essential parameters such as bilayer phase diagrams, mechanical moduli, and the bilayer behaviour upon cargo inclusion and remodelling.

The author demonstrates that bolalipid bilayers behave as binary mixtures, containing bolalipids organized either in a straight conformation, spanning the entire bilayer, or in a u-shaped one, confined to a single leaflet. This dynamic mixture allows bolalipid bilayers to be very sturdy but also provides remodelling. However, remodelling is energetically more expensive than with standard lipids. The authors speculate that this might be why lipids were more abundant in the evolutionary process. Strengths:

This is a wonderful paper, a very fine piece of scholarship. It is interesting from the point of view of biology, biophysics, and material science. The authors mastered the modelling and analysis of these complex systems. The evidence for their findings is really strong and complete. The paper is written superbly, the language is precise and the reading experience is very pleasant. The plots are very well-thought-out.

Weaknesses:

I would not talk about weaknesses, because this is really a nice paper. If I really had to find one, I would have liked to see some clear predictions of the model expressed in such a way that experimentalists could design validation experiments.

We thank the reviewer for their very kind assessment. We incorporated their recommendations regarding experimental validation in the discussion section, as follows (p.14):

“Our model makes a number of predictions that could be tested by experiment either in cells or in vitro. First, it predicts that a small increase in the fraction of archaeal bilayer lipids should be sufficient to soften a bolalipid-rich membrane. While this could be tested in the future, so far only very few studies have yet reported experimental analysis of archaeal membrane mixtures [18, 50]. Second, we observed that membranes with moderate bolalipid molecular rigidity k_bola exhibit curvature-dependent bending rigidity. To experimentally verify this, one could extrude membrane tethers from cells while controlling for membrane tension. Finally, to get to the core mechanism underlying our findings, it will be important to develop experimental methods that will allow the fraction of U-shaped bolalipid conformers per leaflet to be imaged and measured.”

Reviewer #3 (Public review):

Summary:

The authors have studied the mechanics of bolalipid and archaeal mixed-lipid membranes via comprehensive molecular dynamics simulations. The Cooke-Deserno 3-bead-per-lipid model is extended to bolalipids with 6 beads. Phase diagrams, bending rigidity, mechanical stability of curved membranes, and cargo uptake are studied. Effects such as the formation of U-shaped bolalipids, pore formation in highly curved regions, and changes in membrane rigidity are studied and discussed. The main aim has been to show how the mixture of bolalipids and regular bilayer lipids in archaeal membrane models enhances the fluidity and stability of these membranes.

Strengths:

The authors have presented a wide range of simulation results for different membrane conditions and conformations. For the most part, the analyses and their results are presented clearly and concisely. Figures, supplementary information, and movies very well present what has been studied. The manuscript is well-written and is easy to follow.

We thank the reviewer for the detailed assessment of our work and their constructive feedback.

Major issues

R3.Q1: The Cooke-Deserno model, while very powerful for biophysical analysis of membranes at the mesoscale, is very much void of chemical information. It is parametrized such that it is good in producing fluid membranes and predicting values for bending rigidity, compressibility, and even thermalexpansioncoefficientfallingintheacceptedrangeofvaluesforbilayermembranes. But it still represents a generic membrane. Now, the authors have suggested a similar model for the archaeal bolalipids, which have chemically different lipids (the presence of cyclopentane rings for one), and there is no good justification for using the same pairwise interactions between their representative beads in the coarse-grained model. This does not necessarily diminish the worth of all the authors’ analyses. What is at risk here is the confusion between ”what we observe this model of bolalipidor mixed-membranes do” and ”how real bolalipid-containing archaeal membranes behave at these mechanical and thermal conditions.”.

As the reviewer correctly notes, Cooke and Deserno used a minimal model, devoid of chemical detail, to represent fluid lipid membranes composed of bilayer lipids. Indeed archaeal lipids are chemically different compared to non-archaeal lipids, but just like non-archaeal lipids, they can be very different from one another. Given the chemical diversity of bolalipids between each other, instead of representing their complexity in a complicated model with many experimentally unconstrained parameters, we here defined a minimal model for bolalipids. The power of this minimal model is to represent the key physical/geometrical characteristics of archaeal membranes, namely the fact that lipid heads on two sides of the membrane are often connected, that bolalipids can exhibit a conformational change, and that bolalipids mix with some percentage of bilayer molecules. We then ask a general question: how do these unique geometrical characteristics of archaeal membranes influence their mechanics and reshaping? The reviewer is however right in pointing out that a model, regardless of its level of details (atomistic, coarse-grained, minimal), is still a model.

Our approach of extending an established coarse-grained model for bilayer lipids to bolalipids is further supported by experimental observations, which report that archaeal bilayer lipids can form membranes of comparable bending rigidity to those of non-archaeal bilayer membranes [53]. Hence, different lipid linkages (archaeal vs. non-archaeal) give rise to fluid, deformable membranes of not too dissimilar rigidities, suggesting that both archaeal and non-archaeal bilayer lipids can be represented by a similar minimal coarse-grained model for the purpose of mesoscopic biophysical investigations. Since archaeal bolalipids have the same core chemical structure as two archaeal bilayer lipids joined by their tail ends, similarly we model a bolalipid by joining two bilayer lipids. Such an approach also efficiently enables us to compare bolalipid with bilayer membranes, and connect to the large body of knowledge on the physics of bilayer membranes.

To conclude, our coarse-grained model is indeed intended to capture the main physical properties of bolalipid membranes, and not their chemical diversity.

R3.Q2: Another more specific, major issue has to do with using the Hamm-Kozlov model for fitting the power spectrum of thermal undulations. The 1/q² term can very well be attributed to membrane tension. While a barostat is indeed used, have the authors made absolutely sure that the deviation from 1/q⁴ behaviour does not correspond to lateral tension?

To the casual observer, any 1/q² trend might point at membrane tension. However, the precise functional form is relevant as it determines whether the 1/q² dominates the 1/q⁴ trend for small or large values of the wave number q in the fitted power spectrum.

The first model (including lipid tilt) exhibits the functional form 1/(kq⁴) + 1/(kq²). In contrast, the second model (including membrane tension) exhibits the functional form 1/(kq⁴ + ∑q²). Importantly, the two models obey a different functional form. Here k and k_θ, are the bending and tilt moduli, which are assumed positive, and ∑ is the membrane tension, which can be either positive or negative. For the first model (with tilt), while for small q the amplitude is proportional to q^-4, for large q the amplitude is proportional to q^-2. In contrast, for the second model (with positive tension) while for small q the amplitude is proportional to q^-2, for large q the amplitude is proportional to q^-4. If membrane tension were to be negative in the second model, the slope would cross from negative infinity for small q to -4 for large q. The functional dependencies are summarized in Author response image 1A.

For rigid bolalipid membranes, it is clearly visible that the slope of the power spectrum plotted against the wave number q decreases with increasing q (Author response image 1B). While the slope initially assumes a value close to 4, it gradually approaches 2 for larger values of q. We conclude that only the model including lipid tilt can fit the power spectrum of membrane fluctuations appropriately (solid-dashed line), whereas the model with tension fails to fit the data (dashed line). We note that the combined model containing both lipid tilt and membrane tension does not give a better fit (dotted line).

To demonstrate that the tension model cannot fit the data, we included the best fits for both models for rigid bolalipid membranes in the new SI section 16 (p. S22) and show that only the tilt model leads to acceptable fits. We also measured the projected membrane tension - , where P_x,P_y are respectively the pressure in x and y direction and  L_z is the dimension of the simulation box in z axis. We found the projected membrane tension to give a negligible value similarly to the one that we indirectly measured by fitting a combined model with both tension and tilt, further confirming our conjecture.

Author response image 1.

(A) Schematic showing the decay of the power spectrum as a function of the wave number q in the tilt model (top), in the tension model with positive membrane tension (middle), and in the tension model with negative membrane tension (bottom). (B) Fitted power spectrum as a function of q for rigid bolalipid membranes (k_bola=5k_BT). The fit shows that while the model with tension (dashed line) cannot fit the data, the model with tilt nicely fits the spectrum (solid-dashed line). The combined model including both tension and tilt does not fit the spectrum any better (dotted line).

R3.Q3: I got more worried when I noticed in the SI that the simulations had been done with combined ”fix langevin” and ”fix nph” LAMMPS commands. This combination does not result in a proper isothermal-isobaric ensemble. The importance of tilt terms for bolalipids is indeed very interesting, but I believe more care is needed to establish that.

In what follows, we show that there is no reason to worry. First of all we want to clarify that the physical setup we simulate is that of a membrane contained in a heat bath under negligible tension with correct diffusional dynamics. To achieve this physical setup, for which we use a Langevin thermostat combined with pressure control via an overdamped barostat, which we implement in LAMMPS by combining ”fix langevin” and ”fix nph”.

In more detail: we simulated particles in an implicit solvent, for which we use a Langevin thermostat to get the right diffusional dynamics. To apply the theory of fitting fluctuation spectrums the simulation box length needs to be (near) constant. However, simulating membranes at a fixed box size results in an average non-zero membrane tension, making it hard to measure bending rigidity. The reason is that the effect of membrane tension is most influential on the largest wavelength modes, which are also most decisive when determining mechanical membrane properties like membrane rigidity. To minimize the effect of tension, we perform our simulation with an overdamped barostat (𝜏_baro = 10 𝜏 _langevin), which keeps the membrane near tensionless, as also done before [32]. In the revised manuscript, we have clarified the statement on the physical ensemble used (p.S2):

“For simulating flat membrane patches of bolalipids, we combined the previously used Langevin thermostat with relaxation time of 1𝜏 with a Nosé–Hoover barostat with relaxation time of 10𝜏. In LAMMPS this amounts to combining the commands ’fix langevin’ with ’fix nph’. We configured the barostat to set lateral pressure P_xy to zero by re-scaling the simulation box in the x-y plane. We compare this setup to a fixed box length setup, and an NPT ensemble setup, in SI section 17.”

To connect our results with statistical mechanics ensemble theory we tested alternative setups. Similar setups, including the formal isothermal-isobaric ensemble, where N,P,T are kept constant using Nose-Hoover style equations for thermostating and barostating with modern corrections [34], which the reviewer refers to, result in very similar fluctuation spectrums. Consequently, our measurements of bending and tilt modulus hold true regardless of the integration scheme. However, such a setup does not correctly capture implicit solvent and diffusional dynamics.

In even more detail: we tested our setup (implemented via ”fix langevin”+”fix nph”) versus a isothermal-isobaric ensemble (implemented via ”fix npt”). We measured volume mean and standard deviation, and found them matching for a reference LJ gas.

To be completely sure, and to please the reviewer, we have performed additional verifications in the new SI section 17, which we summarize in the following. We simulated three representative membranes with different integration schemes: ”fix npt”, ”fix langevin”+”fix nph”, and ”fix langevin” (Langevin dynamics with projected area fixed at the average value obtained from a ”langevin+nph”). We checked that the ”fix nph” barostat is merely equilibrating the membrane to a tensionless configuration, after which the projected membrane area (A_p = L_xL<sub<y</sub>) is practically constant. Consequently, the different schemes resulted in minor changes in the longest wavelength modes that we tracked down to small changes in the negligible tension. The resulting measurements of bending modulus change by less than 10%, and our main text conclusions do not change. Author response image 2 compares the fluctuation spectrums for the different integration schemes.

Author response image 2.

Height fluctuation spectrum, for a bilayer membrane at T_eff =1.1, simulated with Langevin dynamics (pink, ‘langevin‘), our setup (purple, ‘nph+langevin‘), and under an isothermal-isobaric ensemble (blue, ‘npt‘); fits are shown as dotted lines.

R3.Q4: This issue is reinforced when considering Figure 3B. These results suggest that increasing the fraction of regular lipids increases the tilt modulus, with the maximum value achieved for a normal Cooke-Deserno bilayer void of bolalipids. But this is contradictory. For these bilayers, we don’t need the tilt modulus in the first place.

We understand the concern why this might be counter-intuitive, and we thank the reviewer for pointing it out. We first want to stress that the tilt modulus can also be measured for bilayer membranes even if it is not needed to fit the fluctuation spectrum. If we measure the tilt modulus for a bilayer membrane, we obtain a value similar to the previously measured one [36]. Importantly, here we also report measurements for the tilt modulus for bolalipid membranes.

To understand the seemingly contradictory behaviour of the tilt modulus, it is insightful to rewrite the expression for the fluctuation spectrum as done in Eq. (1):

where is a characteristic length scale related to tilt, which we call the tilt persistence length. From the last equation it is easy to see that the tilt modulus 𝜅_𝜃 becomes relevant for the fluctuation spectrum if the tilt persistence length l_𝜃  is not negligible. In other words, this means that we have to consider the tilt modulus 𝜅_𝜃 as relevant, if it is sufficiently small compared to the bending rigidity 𝜅.

However, this is not only counter-intuitive, but also difficult to communicate graphically. Per the excellent reviewer’s suggestion, to make the interpretation more accessible, we converted in the main text and its figures the tilt modulus to the more directly interpretable tilt persistence length l_𝜃, as this is small when tilt is irrelevant (for bilayer lipids and flexible bolalipids) and large otherwise (for rigid bolalipids). This includes changes to the main text on p.6 and p.8 , and to the insets in Figs. 2C and 3B. We note that for completeness we also report the tilt modulus 𝜅_𝜃  in the SI.

R3.Q5: Also, from the SI, I gathered that the authors have neglected the longest wavelength mode because it is not equilibrated. If this is indeed the case, it is a dangerous thing to do, because with a small membrane patch, this mode can very well change the general trend of the power spectrum. As a lot of other analyses in the manuscript rely on these measurements, I believe more elaboration is in order.

We thank the reviewer for the careful examination of our supplementary material. For each fluctuation spectrum measurement, we ran multiple replicas. We observed that the largest wavelength modes were not fully equilibrated. In the simulations the first mode of the fluctuation spectrum is probed at different amplitudes and phases. We thus expected the potential systematic error would show up clearly when comparing spectrums of the different replicas. As we saw no correlation in these systematic offsets between replicas, we concluded that the simulations are sufficiently equilibrated and we could safely exclude the first mode of the fluctuation spectrum from our analysis.

To show without doubt that this procedure does not randomly bias our results, we also ran simulations for three representative membranes until all modes were equilibrated. On the modes previously equilibrated, the resulting spectrums agree with our previous shorter simulations. On the largest wavelength modes that were previously not fully equilibrated, we noticed a small deviation from theory, specifically for flexible membranes (small bending modulus). These small deviations can be explained by including a negligible negative tension. Importantly, however, the resulting bending modulus σ stays nearly the same. We note that the small negative tension disappears when we halve the timestep (see Author response image 3). This verification is shown in SI section 17.

R3.Q6: The authors have found that ”there is a strong dependency of the bending rigidity on the membrane mean curvature of stiffer bolalipids.” The effect is negative, with the membrane becoming less stiff at higher mean curvatures. Why is that? I would assume that with more flexible bolalipids, the possibility of reorganization into U-shaped chains should affect the bending rigidity more (as Figure 2E suggests). While for a stiff bolalipid, not much would change if you increase the mean curvature. This should be either a tilt effect, or have to do with asymmetry between the leaflets. But on the other hand, the tilt modulus is shown to decrease with increasing bolalipid rigidity. The authors get back to this issue only on page 10, when they consider U-shaped lipids in the inner and outer leaflets and write, ”this suggested that an additional membrane-curving mechanism must be involved.” But then again, in the Discussion, the authors write, ”It is striking that membranes made from stiffer bolalipids showed a curvature-dependent bending modulus, which is a clear signature that bolalipid membranes exhibit plastic behaviour during membrane reshaping,” adding to the confusion.

Author response image 3.

Height fluctuation spectrum, for a bilayer membrane at T_eff =1.1, as simulated in the main text (grey, for 60⇥10³τ), for longer duration (1_.44⇥10⁶τ) (pink), and with the longer duration and halved timestep =0.005_τ(purple); fits are shown as dotted lines (tension and tilt) or dash-dot lines (tilt only).

We thank the reviewer for asking this important question. Membrane bending rigidity in bolalipid membranes decreases dramatically once a small fraction of U-shapes is allowed to form, but then plateaus once this U-shape fraction reaches 20%. In a curved bolalipid membrane, U-shapes must accumulate in the outer leaflet to accommodate for area difference. Together, the bending rigidity non-linear dependence on U-shape fraction, and the promotion of U-shapes by curvature, explain why in a membrane made of moderately stiff bolalipids (k_bola = 1k_BT), which contain very few U-shapes in the flatstate, the bending rigidity of the membrane decreases as curvature increases. While in a membrane made of flexible bolalipid molecules (k_bola = 0), where many U-shapes are present in the flat membrane, the bending rigidity does not change with curvature.

Bending rigidity 𝜅 in flat membranes composed of bolalipids decreases dramatically once a small fraction of U-shapes is allowed to form, but plateaus once more than 20% of U-shaped bolalipids are present. In details, our data shows that with an increasing bolalipid molecular rigidity k_bola, both the number of U-shaped bolalipids decreases (Fig. 2B) and the membrane rigidity 𝜅 increases (Fig. 2C). Thus, the correlation suggests that U-shaped bolalipids soften the membrane, in a non-linear way where most of the change in membrane bending rigidity happens for U-shaped bolalipid fraction < 20% (Figure S11).

Separately, membrane curvature affects the area difference between curved membrane leaflets and thus drives U-shape accumulation. To be specific, a cylindrical membrane with area A, mean curvature H and thickness h has the outer leaflet with area A(1 + Hh) and the inner leaflet with smaller area A(1 Hh). This can be large, in our simulations up to an area change of Hh \= 25%. For pure bolalipid membranes, straight bolalipids occupy the same space in each leaflet. Area difference can then be achieved only by having a different amount of U-shaped bolalipids in each leaflet, which can result in a different U-shape fraction between leaflets and thus ’asymmetry between leaflets’. Figure S10 confirms U-shape head fraction asymmetry that increases with curvature, for both flexible (k_bola = 0) and moderately stiff bolalipids (k_bola = 1k_BT).

Together, these two effects result in membrane softening under curvature for the moderately stiff bolalipids, but constant rigidity for flexible bolalipids (Fig. 2F). In details: for membranes composed of moderately stiff bolalipid molecules (k_bola = 1k_BT), the U-shape bolalipid head fraction only increases in the outer leaflet, goingfrom10to20%(Figure S10). This is in the high sensitivity region where the bending rigidity is expected to change the most (Figure S11). We hypothesize that the molecular rigidity of a U-shaped bolalipid creates compression on the outer leaflet that stabilizes the membrane curvature and thus causes membrane softening. We suspect that for membranes composed of rigid bolalipids (k > 1k_BT), the effect is likely not present due to the absence of U-shape formation even under strong bending.

By contrast, for membranes composed of flexible bolalipids (k = 0), the U-shaped bolalipid head fraction changes relatively little from its value for flat membranes (from 50% to respectively 60 and 40% for the outer and inner leaflet, Figure S10). This is in the region where the membrane bending rigidity is expected to respond weakly to U-shape fraction (Figure S11). Additionally, the change is symmetric, so presumably the outer leaflet becomes softer as the inner leaflet becomes stiffer, thus creating opposing effects and only weakly affecting the membrane bending rigidity as a whole. We note that the distinction between the U-shape head fraction that we plot (Figure S10) and U-shape fraction (Figure S11) matters little for this analysis.

We have added this deduction and its plots to SI section 8, and revised the corresponding statement in the main text accordingly (p.7 ).

“Changing membrane curvature alters the area differently in the two membrane leaflets. To adapt to the area difference, we thus expect the fraction of U-shaped bolalipids to change as the membrane curvature changes. Moreover, the results of Fig. 2B and Fig. 2C showed that the U-shaped bolalipid fraction and the membrane bending rigidity are correlated. As a result, we predict that the fraction of straight versus U-shaped bolalipids in a membrane will change in response to membrane bending, in a way that makes the bending rigidity of a bolalipid membrane curvature dependent.”

R3.Q7: This issue is repeated when the authors study nanoparticle uptake. They write: ”to reconcile these seemingly conflicting observations we reason that the bending rigidity, similar to Figure 2F, is not constant but softens upon increasing membrane curvature, due to dynamic change in the ratio between bolalipids in straight and U-shaped conformation. Hence, bolalipid membranes show stroking plastic behaviour as they soften during reshaping.” But the softening effect that they refer to, as shown in Figure 4B, occurs for very stiff bolalipids, for which not much switching to U-shaped conformation should occur.

We thank the reviewer for locating a particularly dense sentence. We changed the text to explicitly refer to the range k 2 [0,2] k_BT for which there is significant change in U-shape fraction (p.8 ):

“To reconcile these seemingly conflicting observations we reason that the bending rigidity κ, similar to Fig. 2F, is not constant but softens in the range k 2 [0,2] k_BT, upon increasing membrane curvature. This is due to the dynamic change in the ratio between bolalipids in straight and U-shaped conformation.”

As for Fig. 4B, for k > 2k_BT, pores form thus explaining the plateau in adsorption energy.

R3.Q8: Another major issue is with what the authors refer to as the ”effective temperature”. While plotting phase diagrams for kT/eps value is absolutely valid, I’m not a fan of calling this effective temperature. It is a dimensionless quantity that scales linearly with temperature, but is not a temperature. It is usually called a ”reduced temperature”. Then the authors refer to their findings as studying the stability of archaeal membranes at high temperatures. I have to disagree because eps is not the only potential parameter in the simulations (there are at least space exclusion and angle-bending stiffnesses) so one cannot identify changing eps with changing the global simulation temperature. This only works when you have one potential parameter, like an LJ gas.

We indeed thought about this before and found that it makes little difference in our set-up. To thoroughly show that the distinction matters very little, per reviewer’s question, we computed our phase diagrams by scaling temperature T explicitly (and not lipid tail interactions T_eff = k_BT /ϵ_p). We added these results to the SI section 14 and found no significant difference when comparing scaling tail interactions (Figure S15A) with scaling temperature explicitly (Figure S15B).

We also computed Fig. 2A-C for scaling interactions (Figure S17A) and scaling temperature explicitly (Figure S17B). We found a slightly increased U-shaped bolalipid fraction for low k when comparing scaling interactions (Figure S17A) with temperature scaling (Figure S17B). The reason is that the U-shaped fraction depends on temperature, as with higher temperature bolalipids can easier transition into the U-shape. Most importantly, however, we found no qualitative changes on the liquid region or the mechanical membrane properties when we compared the different scaling variants.

The reason why both scaling variants match so well can be understood easily. All pair potentials, including volume exclusion interactions between head beads and other membrane beads, were also scaled in the same manner as tail-to-tail interactions, as described in the SI. In contrast, the energy scales for maintaining the lipid bonds, the bilayer lipid angles and the bolalipid angles are relatively large compared to the energy scales involved in tail-to-tail interactions. This separation of energy scales guarantees that there will be little effect when increasing global temperature. Regarding nomenclature, we take the reviewer’s advice and have added ’reduced temperature’ as an alias for T_eff in the main text.

In the revised version of the manuscript, we mention these observations in the SI section 14 and point towards these results in the main text (p.4 ):

“This interaction strength governs the membrane phase behaviour and can be interpreted as the effective temperature or reduced temperature T_eff = k_BT /ϵ_p. As the distinction between scaling interactions (T_eff) or temperature (T) is not important for our analysis (see Supplemental Information (SI) section 14), for simplicity we refer to T_eff as temperature in the following.”

Minor issues

R3.Q9: As the authors have noted, the fact that the membrane curvature can change the ratio of U-shaped to straight bolalipids would render the curvature elasticity non-linear (though the term ”plastic” should not be used, as this is still structurally reversible when the stress is removed. Technically, it is hypoelastic behaviour, possibly with hysteresis.) With this in mind, when the authors use essentially linear elastic models for fluctuation analysis, they should make a comparison of maximum curvatures occurring in simulations with a range that causes significant changes in bolalipid conformational ratios.

We thank the reviewer for their suggestion on calling the non-linear behaviour of the curvature elasticity hypoelastic. We have edited the main text accordingly (p.8 ):

“In an elastic material, the strain modulus holds constant and deformation is reversible. For bolalipid membranes at k = 1k_BT, however, the bending modulus decreases when deformation increases, rendering bolalipid membranes hypoelastic.”

Moreover, regarding the maximum curvatures occurring in the fluctuation simulations: We first note that the ensemble average of the mean curvature H from the fluctuation measurements is indicated as a vertical line in Fig. 2F. As the average value is nearly zero, the membrane can be considered as flat in good approximation. To investigate the question in more detail, we extended the SI with a careful analysis of the validity of the maximum membrane curvature and the validity of the Monge gauge approximation (SI section 15).

In short, we found that the involved membrane curvatures are small and therefore are unlikely to trigger any significant changes of the bending modulus. Moreover, since we are dealing with two bolalipid conformations, we also tested the homogeneity of the membrane. In our simulations of flat membrane patches we did not observe clustering or phase separation between the two bolalipid conformations beyond the [2,3]σ range. Furthermore, we get good agreement between our fluctuation measurement and the cylinder simulations in Fig. 2F. We now mention this verification in the revised version of the manuscript (p.8 ):

“Fortunately, this dependency on curvature does not invalidate our fluctuation results, where the curvature is small enough that its effect on the bending modulus is negligible (SI section 15).”

Last but least, simulating bending/unbending cycles of an arc-shaped membrane (frozen endpoints) shows agreement with cylinder membrane simulations, and no hysteresis at the rates of deformation employed (cf. M. Amaral’s thesis [54], soon to be out of the embargo period).

R3.Q10: The Introduction section of the manuscript is written with a biochemical approach, with very minor attention to the simulation works on this system. Some molecular dynamics works are only cited as existing previous work, without mentioning what has already been studied in archaeal membranes. While some information, like the binding of ESCRT proteins to archaeal membranes, though interesting, helps little to place the study within the discipline. The Introduction should be revised to show what has already been studied with simulations (as the authors mention in the Discussion) and how the presented research complements it.

The present research for the first time covers archaeal membranes with a single coarse-grained model capable of assuming both bolalipid in-membrane conformations and sweeps through temperature, membrane composition, and molecular rigidity. The work shows the first curvature dependent bending modulus for pure bolalipid membranes. It also investigates systematically bending modulus and Gaussian modulus, and tests the model in an all-encompassing budding simulation that incorporates topology changes. Existing atomistic or coarse-grained MD simulations (MARTINI or similar force fields) are limited to small patches of membrane, with no study of large-scale deformations or topology changes; plus, they rely on force fields that were parametrized for bilayer membranes.

To give a comprehensive overview of the field, we revised the introduction section of the manuscript, in which we now discuss previous computational work investigating membrane diffusivity, U-shaped lipid fraction, and bending rigidity (p.3 ):

“By contrast, only a few studies have investigated bolalipid membranes applying computational or theoretical tools [24, 25]. Specifically, the pore closure time in bolalipid membranes, and the role of cyclopentane rings for membrane properties has been investigated using all-atom simulations, showing decreased lateral mobility, reduced permeability to water, and increased lipid packing [26–28]. Moreover, using coarse-grained simulations, it was suggested that bolalipid membranes are thicker [29], exhibit a gel-to-liquid phase transition at higher temperature [30], and exhibit a reduced diffusivity [31]. However, little research has been devoted to investigating mechanics and reshaping of bolalipid membranes at the mesoscale despite the obvious importance of this question from evolutionary, biophysics, and biotechnological perspectives and although different membrane physics is expected to manifest.”

Following the reviewer’s advice and to keep the introduction concise and focused on bolalipid membranes, we have removed the paragraph on ESCRT-III proteins in the revised manuscript.

R3.Q11: The authors have been a bit loose with using the term ”stability”. I’d like to see the distinction in each case, as in ”chemical/thermal/mechanical/conformational stability”.

We have clarified when applicable the type of stability throughout the manuscript. In all other instances, if not clear from context, we mean simply that the membrane persists being a membrane. At our coarse-grained level, this means the membrane does not disassemble into a gas phase.

R3.Q12: In the original Cooke-Deserno model, a so-called ”poorman’s angle-bending term” is used, which is essentially a bond-stretching term between the first and third particle. However, I notice the authors using the full harmonic angle-bending potential. This should be mentioned.

This is made clear in the SI (Eq. (S3)). Cooke and Deserno mention the harmonic angle potential as a valid alternative in their original publication. We now also added this detail to the main text (p.3 ):

“The angle formed by the chain of three beads is kept near 180° via an angular potential with strength k₀, instead of the approximation by a bond between end beads of the original model [32].”

R3.Q13: The analysis of energy of U-shaped lipids with the linear model E \= c₀ + c₁k is indeed very interesting. I am curious, can this also be corroborated with mean energy measurements? The minor issue is calling the source of the favorability of U-shaped lipids ”entropic”, while clearly an energetic contribution is found. The two conformations, for example, might differ in the interactions with the neighbouring lipids.

We were also curious and thank the reviewer for the suggestion of mean energy measurements. We concluded that there must be either an entropic contribution to the free energy or an intermolecular interaction energy favouring U-shaped bolalipids. We have now included these measurements in SI section 6 (p.S5 ):

“By splitting the average potential energy between an internal contribution (bonds, angles and pair interactions between particles in the same molecule) and an external contribution (pair interactions between a molecule and its neighbours), we determined the transition energy from straight to U-shaped bolalipids in detail. We found that this transition lowers the internal potential energy of the bolalipid while increasing its interaction energy. In total, we obtained an energy barrier for the transition of ΔE_s→u = 0.79±0.01k_BT. Since the fit indicates, however, that the U-shaped bolalipid conformation is preferred over the straight conformation, we conclude that there must be either an entropic contribution to the free energy or an intermolecular interaction energy favouring U-shaped bolalipids.”

We refer to these measurements in the main text (p.6 ):

“For the fit it appears that c₀ < 0, which implies that bolalipids in U-shape conformation are slightly favoured over straight bolalipids at k = 0 (explored in SI section 6).”

R3.Q14: The authors write in the Discussion, ”In any case, our results indicate that membrane remodelling, such as membrane fission during membrane traffic, is much more difficult in bolalipid membranes [34].” Firstly, I’m not sure if studying the dependence of budding behaviour on adhesion energy with nanoparticles is enough to make claims about membrane fission. Secondly, why is the 2015 paper by Markus Deserno cited here?

We thank the reviewer for giving us the opportunity to clarify. We make an energetic argument on membrane fission based on the observed difference in the ratio of .

Splitting a spherical membrane vesicle into two spherical vesicles (fission) increases the bending energy by 8𝜋𝜅 and decreases the energy related to the Gaussian bending modulus by . The second part of the argument is given for example in the review by Markus Deserno (p.23, right column), that’s why we cite the paper here. Together, this gives an energy barrier, required for membrane fission in the considered geometry of ∆E_fission = . We found that is around 0.5 for bolalipid membranes and around 1 for bilayer membranes. Since 𝜅 was typically larger in bolalipid membranes we thus expect the energy barrier for fission ∆E_fission to be larger for bolalipid membranes. We therefore predict that membrane remodelling, such as membrane fission during membrane trafficking, is harder in bolalipid membranes. We explain our reasoning in the discussion of the revised manuscript (p.13 ):

“Membrane remodelling, such as the fission of one spherical vesicle into two, increases the bending energy by 8πκ but decreases the energy related to the Gaussian modulus by – [39], giving rise to a fission energy barrier of ∆E_fission = . Our results indicated that while in bolalipid membranes 𝜅 is larger, is smaller compared to bilayer membranes. Our results thus predict a larger energy barrier for membrane fission ∆E_fission in bolalipid membranes compared to bilayer membranes.”

R3.Q15: In the SI, where the measurement of the diffusion coefficient is discussed, the expression for D is missing the power 2 of displacement.

We thank the reviewer for spotting this oversight. We corrected it in the revised version of the SI (p.S5 ).

R3.Q16: Where cargo uptake is discussed, the term ”adsorption energy” is used. I think the more appropriate term would be ”adhesion energy”.

For the sake of simplicity, we changed the term to adhesion energy (caption of Fig. 4, and p.10). We do not have a strong opinion on this, but we believe that adsorption energy would be equally correct as we describe the adsorption of many lipid head beads to a nanoparticle.

R3.Q17: Typos:

Page 1, paragraph 2: Adaption → Adaptation. Page 10, paragraph 1: Stroking → Striking.

We thank the reviewer for spotting these typos which we have corrected in the revised version of the manuscript.

Recommendations for the authors

Reviewer #1 (Recommendations for the authors):

A few thoughts (likely out of the scope of this paper but possibly to consider upon revision):

R1.Q1: Do bolalipids always have the same headgroup? I don’t recall reading this in the introduction/discussion. R1 and R2 are in Figure 1, but I don’t know whether there are standard types. Could this be expanded upon? Is the model able to take these differences into account?

We thank the reviewer for raising this important question. Similar to bacteria and eukaryotes, in archaea there is a huge variety in terms of the different head groups that lipids can contain and thus also lipid variety. Most archaeal lipids have head groups that contain either phosphate groups or sugar residues. Typically, archaeal bolalipids are asymmetric and contain a phosphatidyl and a sugar moiety at the two ends of the lipid molecule. Within the membrane the lipid is oriented such that the phosphatidyl moiety points towards the interior of the cell whereas the sugar moiety points towards the outside of the cell as it occupies more space [5].

In our computational model, however, we consider symmetric bolalipids for the sake of simplicity and to decouple the role of ”connected geometry” from other effects. In principle, we could investigate the effect of lipid asymmetry by increasing the size of one of the lipid head beads. However, this investigation exceeds the scope of the present study and therefore requires future work.

In the revised version of the manuscript, we now clarify that bolalipids can have different headgroups (p.1 and the caption of Fig. 1):

“The hydrophilic heads can be composed of different functional groups with phosphatidyl and sugar being the most relevant moieties. For bolalipids the two head groups at either end of the molecule are typically distinct (Fig. 1A right) [5].”

“The hydrophilic head of a bolalipid can be composed of different functional groups represented by R1 and R2 (right).”

We also explicitly state that we neglect lipid head group asymmetry for the sake of simplicity (p.4 ):

“To decouple the effect of the connected geometry of the bolalipids from that of lipid asymmetry, we assume both head beads of a bolalipid to share the same properties.”

R1.Q2: Is it possible to compare the mesoscale models to either Coarse-grained or even all-atom lipid models? Have simulations previously been performed for bolalipids at those levels of description?

A few studies have investigated bolalipids membranes in simulations previously. These studies either used all-atom or coarse-grained simulations. However, none of these studies investigated how bolalipids respond to membrane deformations. Therefore, it is currently not possible to directly compare our results to studies in the literature. However, to recapitulate our predictions experimentally is certainly something that could and should be done in the future. As a reply to this reviewer and reviewer 3, we discuss the current state of modelling bolalipid membranes in simulations in the revised version of the manuscript (p.3 ):

“By contrast, only a few studies have investigated bolalipid membranes applying computational or theoretical tools [24, 25]. Specifically, the pore closure time in bolalipid membranes, and the role of cyclopentane rings for membrane properties has been investigated using all-atom simulations, showing decreased lateral mobility, reduced permeability to water, and increased lipid packing [26–28]. Moreover, using coarse-grained simulations, it was suggested that bolalipid membranes are thicker [29], exhibit a gel-to-liquid phase transition at higher temperature [30], and exhibit a reduced diffusivity [31]. However, little research has been devoted to investigating mechanics and reshaping of bolalipid membranes at the mesoscale despite the obvious importance of this question from evolutionary, biophysics, and biotechnological perspectives and although different membrane physics is expected to manifest.”

We want to mention, however, that we do compare membrane diffusivity, U-shaped lipid fraction, and bending rigidity to the behaviour and values that have been previously measured in simulations in the discussion section. In general, we find good agreement between our results and previously reported behaviour/values (p.13 ):

“While flexible bolalipid membranes are liquid under the same conditions as bilayer membranes, we found that stiff bolalipids form membranes that operate in the liquid regime at higher temperatures. These results agree well with previous molecular dynamics simulations that suggested that bolalipid membranes are more ordered and have a reduced diffusivity compared to bilayer membranes [24, 29]. In our simulations, this is due to the fact that completely flexible bolalipids molecules adopt both straight (transmembrane) as well as the U-shaped (loop) conformation with approximately the same frequency. In contrast, stiff bolalipids typically only take on the straight conformation when assembled in a membrane. These results agree with the previous coarse-grained molecular dynamics simulations using the MARTINI force field which showed that the ratio of straight to U-shaped bolalipids increased upon stiffening the linker between the lipid tails [29].

[...]

When we determined the bending rigidity of bolalipid membranes by measuring their response to thermal fluctuations, we found that membranes made from flexible bolalipids are only slightly more rigid than bilayer membranes. This result is consistent with previous atomistic simulations, which showed that the membrane rigidity was similar for membranes composed of bilayer lipids and flexible synthetic bolalipids [45].”

R1.Q3: How would membrane proteins alter the behaviour of bolalipids? Either those integral to the membrane or those binding peripherally?

The reviewer asks an important question. However, the question is difficult to answer due to its scope and the gaps in the current literature. Important examples of integral or peripheral membrane proteins that alter the behaviour of bolalipids and archaeal bolalipid membranes are involved in cell homeostasis, cell division, membrane trafficking, and lipid synthesis.

The cells of many archaeal species are enclosed in a paracrystalline protein layer called the Slayer, which is attached to the lipid membrane [4, 55]. The main function of the S-layer is to keep the cell’s shape and to protect it against osmotic stress. Due to the embedding of the S-layer in the membrane at specific locations, it is to be expected that the membrane properties are influenced by the S-layer. Furthermore, archaea execute cell division by locally reshaping the membrane using FtsZ and ESCRT-III proteins [56]. While Asgard archaeal genomes encode proteins with homology to those regulating aspects of eukaryotic membrane remodelling and trafficking [57], they have yet to be observed undergoing a process like endocytosis [58]. In addition, it has been speculated that the proteins that drive the synthesis of two diether lipids into a tetraether lipid are either membrane associated or integral membrane proteins [59].

However, to the best of our knowledge it is not known how membrane proteins specifically alter the behaviour of bolalipids. Future work will need to be executed to answer this question. Following the advice of reviewer 3 and to keep the introduction concise and focused on bolalipid membranes, we do not mention these observations in the revised manuscript.

R1.Q4: Is there a mechanism in cells to convert or switch bolalipids from a straight to a u-shaped description? Does this happen spontaneously or are there enzymes responsible for this?

We thank the reviewer for bringing up this important point. Despite the relevance of the question, little is currently known about the mechanism that make bolalipids transition between a straight and a U-shaped configuration mainly because there is to date no established experimental method.

Besides our own results, most of what we know comes from coarse-grained molecular dynamics simulations, which showed that bolalipids can spontaneously transition between the straight and U-shaped configuration [29]. In addition, by using comparative genomic analysis, it has been predicted that many archaeal species contain flippases, i.e., membrane proteins that are able, upon the consumption of energy, to transfer (flipflop) bilayer lipids between the two membrane leaflets [43]. Moreover, it has been shown that Halobacterium salinarum (an archaeon with a bilayer lipid membrane) [44] contains scramblases, which are membrane proteins that passively transfer bilayer lipids from one membrane leaflet to the other. It is therefore tempting to speculate that similar proteins might exist for bolalipids which could facilitate the straight to U-shaped transition.

In addition, it has been reported that vesicles composed of bolalipid membranes can undergo fusion with enveloped influenza viruses [17]. In this context, it has been suggested that the influenza fusion protein hemagglutinin may locally induce U-shaped bolalipids to facilitate membrane fusion. However, all these hints are by far no proof of a mechanism that can drive the straight to U-shaped bolalipid transition, and further work needs to be done to investigate this question in detail.

In the revised version of the manuscript, we now discuss what is known about potential mechanisms to facilitate the straight to U-shaped transition in the discussion section (p.13 ):

“While previous coarse-grained simulations predicted that bolalipids spontaneously transition between the straight and U-shaped conformations [29], how this happens in archaeal membranes and whether membrane proteins are involved in this conformational transition needs to be clarified in the future. Experimental studies suggest that archaeal membranes contain flippases and scramblases for the transitioning of bilayer lipids between membrane leaflets [43, 44], raising the possibility that similar proteins could also facilitate conformational transitions in bolalipids. In addition, it has been suggested that the viral fusion protein hemagglutinin could cause a transition from straight to U-shaped bolalipid conformation during the fusion of bolalipid vesicles with influenza viruses [17]. However, future investigation is required.”

R1.Q5: Ideally, coordinates and any parameter files required to run the molecular simulations should be included for reproducibility.

We absolutely share the reviewer’s concern with reproducibility and as such have included in the original submission as part of our data availability section a link to a code repository (available at: https://doi.org/10.5281/zenodo.13934991 [51]) that allows initializing and simulating flat membrane patches, with user control of the parameters explored in this paper (𝜔,T_eff,k_bola,f^bi).

Reviewer #2 (Recommendations for the authors):

This is a great paper and I congratulate the authors for writing such a fine piece of scholarship. The only nitty-gritty feedback that I have is summarized in the following three points:

R2.Q1: In the introduction the authors talk about archaea adapting their membrane to retain membrane fluidity. However, homeoviscous adaptation is also fundamental in bacteria and eukaryotes.

The reviewer is correct, like archaea the membranes of bacteria and eukaryotes must balance between flexibility and stability. Moreover, the cell membranes in all 3 domains of life need to maintain membrane fluidity and provide mobility to the embedded lipids and membrane proteins (homeoviscous adaptation). The general idea is that these organisms change the ratio of different lipids to change membrane properties and thereby optimally adapt to their environments [10]. Importantly, however, there are differences of how homeoviscous adaptation is maintained across the different domains of life. As a reply to this reviewer and reviewer 3, we now discuss the underlying mechanisms in the revised parts of the introduction (p.1 ):

“Like for bacteria and eukaryotes, archaea must keep their lipid membranes in a fluid state (homeoviscous adaptation). This is important even under extreme environmental conditions, such as hot and cold temperatures, or high and low pH values [7]. Because of this, many archaea adapt to changes in their environment by tuning the lipid composition of their membranes: altering the ratio between bola- and bilayer lipids in their membranes [8, 9] and/or by changing the number of cyclopentane rings in their lipid tails, which are believed to make lipid molecules more rigid [5]. For example, Thermococcus kodakarensis increases its tetraether bolalipid ratio from around 50% to over 80% when the temperature of the environment increases from 60 to 85 C [10]. Along the same lines, the cell membrane of Sulfolobus acidocaldarius, can contain over 90 % of bolalipids with up to 8 cyclopentane rings at 70 C and pH 2.5 [5, 11]. It is worth mentioning that in exceptional cases bacteria also synthesise bolalipids in response to high temperatures [12], highlighting that the study of bolalipid membranes is relevant not only for archaeal biology but also from a general membrane biophysics perspective.”

R2.Q2: Uncertainties in Gaussian rigidity modulus estimates are not properly reported.

The large uncertainties in the Gaussian rigidity modulus were due to the fact how they were calculated. In short, is determined in cap folding simulations [41] (SI section 9), by using the measured values of the dimensionless parameter 𝜉, related to the folding probability, the bending modulus 𝜅, the membrane line tension , and the cap radius R. In our case, the main source of uncertainty for determining comes from the uncertainty in the measurement of the bending rigidity 𝜅. To obtain 𝜅, previously, we fitted fluctuation spectra for different seeds and only then averaged the obtained values. In the revised version of the manuscript, we now first pool the fluctuation spectra of the different simulation seeds before we fit all spectra at the same time. This new approach results in smaller uncertainties for the bending rigidity 𝜅 and also the Gaussian rigidity modulus .

As a consistency check, in addition to the simulations that we previously performed at T_eff = 1.3, we have repeated the cap folding and line tension simulations at T_eff = 1.2, resulting in similar values for . In the revised version of the manuscript, we report the newly calculated values and uncertainties for at T_eff  = 1.2 in the main text (p.8 ):

“At T_eff  = 1.2, we obtained = 4.30±0.22kBT and thus a ratio of = 0.89±0.04 for bilayer membranes, similar to what has been reported previously [41]. For flexible bolalipid membranes, we got a slightly smaller value for = 5.04 ± 0.37kBT. Due to the larger bending modulus, however, flexible bolalipid membranes show a significantly smaller ratio = 0.64± 0.04 (k = 0). At larger temperature (Teff = 1.3), the ratio can be even smaller = 0.45 ± 0.07 (see SI section 9).”

In addition, we report the values at T_eff = 1.3 and T_eff = 1.2 in the SI (p.S15 , Tabl. S4):

We have also adapted the discussion of the Gaussian bending modulus accordingly (p.13 ):

“Another marked difference between bilayer and flexible bolalipid membranes is the ratio of the Gaussian rigidity to the bending modulus. Instead of being around 1 as for bilayer membranes [41], it is around 1/2 and therefore only half of that of bilayer lipids.”

Reviewer #3 (Recommendations for the authors):

While I think the bulk of the work presented is useful, some of the issues that I raised in my review are indeed major. Without properly addressing them, it is hard to accept the conclusions of the manuscript. I hope the authors can address them by revising their analysis.

We thank the reviewer for their constructive feedback, which helped us to improve the manuscript. We have addressed all points raised by the reviewer in our detailed point-by-point response to the reviewer (see above). We hope the reviewer will now find it easier to accept our conclusions.

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Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Debeuf et al. introduce a new, fast method for the selection of suitable T cell clones to generate TCR transgenic mice, a method claimed to outperform traditional hybridoma-based approaches. Clone selection is based on the assessment of the expansion and phenotype of cells specific for a known epitope following immune stimulation. The analysis is facilitated by a new software tool for TCR repertoire and function analysis termed DALI. This work also introduces a potentially invaluable TCR transgenic mouse line specific for SARS-CoV-2.

Strengths:

The newly introduced method proved successful in the quick generation of a TCR transgenic mouse line. Clone selection is based on more comprehensive phenotypical information than traditional methods, providing the opportunity for a more rational T cell clone selection.

The study provides a software tool for TCR repertoire analysis and its linkage with function.

The findings entail general practical implications in the preclinical study of a potentially very broad range of infectious diseases or vaccination.

A novel SARS-CoV-2 spike-specific TCR transgenic mouse line was generated.

Weaknesses:

The authors attempt to compare their novel method with a more conventional approach to developing TCR transgenic mice. In this reviewer's opinion, this comparison appears imperfect in several ways:

(1) Work presenting the "traditional" method was inadequate to justify the selection of a suitable clone. It is therefore not surprising that it yielded negative results. More evidence would have been necessary to select clone 47 for further development of the TCR transgenic line, especially considering the significant time and investment required to create such a line.

Based on Supplementary Figure 1A only, we understand the concern of the reviewer. However, the data presented in Supplementary Figure 1A is collected during the first rough screening of clones where only the production of IL-2 and IFN-y was measured as a readout for activation. Thereafter, a large selection of responsive clones was further grown and co-cultured with a dose-titration of the antigenic peptide pool. In this second co-culture, also flow cytometry readouts are included such as CD69 expression (as shown in Supplementary Figure 1B). Finally, a narrower selection of responder clones was co-cultured with the different individual peptides to unravel the specificity of the TCR of the clone. In conclusion, the clone was tested at least three times in three distinct set-ups with multiple different readouts.

However, a good evaluation of a clone in an in vitro setting does not necessarily translate in optimal functioning of the cells in a biological context. For instance, some clones survive better in an in vitro setting than others or have already a more activated profile before stimulation.

(2) The comparison is somewhat unfair, because the methods start at different points: while the traditional method was attempted using a pool of peptides whose immunogenicity does not appear to have been established, the new method starts by utilising tetramers to select T cells specific for a well-established epitope.

Given the costs and time involved, only a single clone could be tested for either method, intrinsically making a proper comparison unfeasible. Even for their new method, the authors' ability to demonstrate that the selected clone is ideal is limited unless they made different clones with varying profiles to show that a particular profile was superior to others.

In my view, there was no absolute need to compare this method with existing ones, as the proposed method holds intrinsic value.

We acknowledge the importance of the well-established hydridoma technology and in no way intended to compare these methods head-to-head, nor do not want to question the validity of the classical methods. The reason why we also wanted to show the failed CORSET8 mouse was to highlight the parts of the TCR generating process which could be rationalized. We again want to emphasize that we do not want to compare methods in any way and recognise that we started from two different bases in terms of clone selection (peptide pool stimulation versus tetramer staining). While the tetramer staining that was employed in the generation of CORSET8 mice allowed to enrich the samples for specific responder clones, this enrichment step is not an absolute requirement for the implementation of the presented method or for the successful generation of a TCR Tg mouse model. An alternative approach could be to use the described method to select for activated and expanded clones upon immunisation and test their reactivity in subsequent steps using peptide stimulation before selecting a receptor. In conclusion, we merely wish to present a novel roadmap for others to use for the generation of their TCR Tg mouse to aid in the selection of the most preferable clone for their purposes.

(3) While having more data to decide on clone selection is certainly beneficial, given the additional cost, it remains unclear whether knowing the expression profiles of different proteins in Figure 2 aids in selecting a candidate. Is a cell expressing more CD69 preferable to a cell expressing less of this marker? Would either have been effective? Are there any transcriptional differences between clonotype 1 and 2 (red colour in Figure 2G) that justify selecting clone 1, or was the decision to select the latter merely based on their different frequency? If all major clones (i.e. by clonotype count) present similar expression profiles, would it have been necessary to know much more about their expression profiles? Would TCR sequencing and an enumeration of clones have sufficed, and been a more cost-effective approach?

The method we present in the paper serves as a proof-of-concept, to be adapted to the researcher’s own needs. We agree with the reviewer that for our intentions with the CORSET8 mice, TCRseq in combination with an enumeration of the clones could also have sufficed and would lower the cost of sequencing. However, we wish to present a roadmap for others to use for the generation of their TCR Tg mouse. Important in this, is that the cellular phenotype, and activation state can be taken into consideration, which might for some projects be essential.  

Nonetheless, we do see clear interclonal differences regarding the expression of “activation” genes, where clone 1 is clearly one of the well activated and interferon producing clones (as shown in Author response image 1). As such, researchers could expand these types of analysis to probe for specific phenotypes of characteristics.

Author response image 1.

(4) Lastly, it appears that several of the experiments presented were conducted only once. This information should have been explicitly stated in the figure legends.

To control for interexperimental variation, every experiment represented in the manuscript has been performed at least two times. We have added the additional information regarding the experimental repetitions and groups in the figure legends.

Reviewer #2 (Public Review):

Summary:

The authors seek to use single-cell sequencing approaches to identify TCRs specific for the SARS CoV2 spike protein, select a candidate TCR for cloning, and use it to construct a TCR transgenic mouse. The argument is that this process is less cumbersome than the classical approach, which involves the identification of antigen-reactive T cells in vitro and the construction of T cell hybridomas prior to TCR cloning. TCRs identified by single-cell sequencing that are already paired to transcriptomic data would more rapidly identify TCRs that are likely to contribute to a functional response. The authors successfully identify TCRs that have expanded in response to SARS CoV2 spike protein immunization, bind to MHC tetramers, and express genes associated with functional response. They then select a TCR for cloning and construction of a transgenic mouse in order to test the response of resulting T cells in vivo following immunization with spike protein of coronavirus infection.

Strengths:

(1) The study provides proof of principle for the identification and characterization of TCRs based on single-cell sequencing data.

(2) The authors employ a recently developed software tool (DALI) that assists in linking transcriptomic data to individual clones.

(3) The authors successfully generate a TCR transgenic animal derived from the most promising T cell clone (CORSET8) using the TCR sequencing approach.

(4) The authors provide initial evidence that CORSET8 T cells undergo activation and proliferation in vivo in response to immunization or infection.

(5) Procedures are well-described and readily reproducible.

Weaknesses:

(1) The purpose of presenting a failed attempt to generate TCR transgenic mice using a traditional TCR hybridoma method is unclear. The reasons for the failure are uncertain, and the inclusion of this data does not really provide information on the likely success rate of the hybridoma vs single cell approach for TCR identification, as only a single example is provided for either.

We refer to comments 2 and 3 of reviewer 1 for an answer to this point.

(2) There is little information provided regarding the functional differentiation of the CORSET8 T cells following challenge in vivo, including expression of molecules associated with effector function, cytokine production, killing activity, and formation of memory. The study would be strengthened by some evidence that CORSET8 T cells are successfully recapitulating the functional features of the endogenous immune response (beyond simply proliferating and expressing CD44). This information is important to evaluate whether the presented sequencing-based identification and selection of TCRs is likely to result in T-cell responses that replicate the criteria for selecting the TCR in the first place.

We agree with the reviewer that the data in the initial manuscript included only a limited in vivo functional validation of the CORSET8 T cells. Therefore, we extended these in vivo readouts and measured IFN-g production, CD69, T-bet expression (as measure for activation) and Ki-67 expression (as alternative readout than CTV for proliferation). In the single cell data, we saw that these markers were more pronounced in the selected clone compared to other clones. We could confirm these findings in vivo, and found a stronger induction of IFN-g, CD69, T-bet and Ki-67 in CORSET8 T cells compared to endogenous CD45.2 cells and even Spike-Tetramer+ CD45.2 endogenous cells. We added these data in Figure 4.

(3) While I find the argument reasonable that the approach presented here has a lot of likely advantages over traditional approaches for generating TCR transgenic animals, the use of TCR sequencing data to identify TCRs for study in a variety of areas, including cancer immunotherapy and autoimmunity, is in broad use. While much of this work opts for alternative methods of TCR expression in primary T cells (i.e. CRISPR or retroviral approaches), the process of generating a TCR transgenic mouse from a cloned TCR is not in itself novel. It would be helpful if the authors could provide a more extensive discussion explaining the novelty of their approach for TCR identification in comparison to other more modern approaches, rather than only hybridoma generation.

By integrating the recent technological advances in single cell sequencing into the generation of TCR Tg mice, possibilities arise to rationalize clone selection regarding clonal size, lineage/phenotype and functional characteristics. Often, the selection process based on hybridoma selection yields multiple epitope specific clones that upregulate CD69 or IL-2, and only minimal functional and phenotypic parameters are checked before prioritizing one clone to proceed with. In our experience, transgenic clones selected in this way sometimes render TCR clones unable to compete with endogenous polyclonal T clones in vivo. Taken all these caveats into account, the novelty we present here is that the researcher is fully able to select clones based on several layers of information without the need for extensive or repeated screening. Moreover, the selection of the TCR Tg clone can be done via the interactive and easily interpretable DALI tool. Owing to the browser-based interactive GUI, immunologists having limited coding experience can effectively analyse their complex datasets.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Regarding Supplementary Figure 1A was the experiment conducted more than once? Clone 47 seems minimally superior to the other clones. Incorporating a positive control, such as the response of the OT-I hybridoma to SIINFEKL, could have provided a benchmark to gauge the strength of the observed responses.

Also, what was the concentration of the peptide used to restimulate the T cells in vitro? High peptide concentrations can lead to non-specific responses. Ideally, a titration should have been performed, perhaps in a subsequent experiment that only tested those clones that responded well initially. Given the resources required to create and maintain a transgenic mouse line, proceeding with the chosen clone based on the data presented seems to carry considerable risk.

The experiment has been performed three times. The data presented in Supplementary Figure 1A is collected during the first rough screening of clones where only the production of IL-2 and IFN-y was measured as a readout for activation. Thereafter, a large selection of responsive clones was further grown and co-cultured with a dose-titration of the antigenic peptide pool. In this second co-culture, also flow cytometry readouts are included such as CD69 expression (as shown in Supplementary Figure 1B). Finally, a narrower selection of responder clones was co-cultured with the different individual peptides to unravel the specificity of the TCR of the clone. In conclusion, the clone was tested at least three times in three distinct set-ups with multiple different readouts.

In Supplementary Figure 1C, no response to stimulation was detected. Ideally, this figure should have included a positive control, such as PMA/Ionomycin or aCD3/CD28 stimulation.

We agree with the reviewer that this experiment should have included a positive control to validate the non-specific responsiveness of the clone and the technical feasibility of the experiment. Unfortunately, the initial CORSET8 line is frozen and is thus not easily available to repeat the experiment.

Can the authors clarify their gating strategy in the legend of In Supplementary Figure 1D?

Plotted cells are non-debris > single cells > viable cells > CD45+. We have added the information to the legend of Supplementary Figure 1D.

In Figure 2, the figure legend should provide more detail on which cells were sorted for the single-cell RNA sequencing analysis. The materials and methods section explains that cells were stained for CD44. Were activated cells then sorted (either tetramer-positive or -negative), plus naïve CD8 T cells from a naïve mouse?

Supplementary Figure 2 contains the detailed gating strategy during the sort for the single cell experiment. We have added additional red gates to the plots to clarify which samples were sent for sequencing. This has been adapted in the figure legends of both Figure 2 and Supplementary Figure 2. 

In Figure 3, Rag1 sufficient transgenic mice display similar numbers of CD4 and CD8 T cells as WT mice in the spleen. Typically, transgenic mice present skewed frequencies of T cells towards the type generated (CD8 in this case), which the authors only found in the thymus of CORSET8 mice. Could this be discussed?

The comment of the reviewer is valid as there is indeed a skewing towards CD8 T cells in the thymi of the CORSET8 mice. We looked back into the data of the experiments and noticed that poor resolution of some markers might have resulted in improper results. We have repeated this and added another T cell marker (TCRbeta) next to the already included CD3e marker. By including both markers, we were able to show that also in spleen the skewing towards the CD8 T cell phenotype is present.

How many repetitions were performed for the experiments in Figures 3D and 3E? How many mice were analyzed for Figure 3E? Please provide this information in the figure legend. Also, include a proper quantification and statistical analysis of the data shown.

New quantification graphs with statistical analysis have been added to Figure 3E. The accompanying figure legend has been adapted. The co-culture displayed in Figure 3D is a representative experiment of two repetitions.

Figure 4C includes 3-4 mice per group. This experiment should have been replicated, and this information should be indicated in the figure legend.

We apologise for omitting this data in the figure legend. The experiment presented in Figure 4A-C has been repeated twice, yielding results following the same trend. We were unable to pool the data as two different proliferation dyes were used in the separate experiments (CFSE and CTV). Furthermore, in the in vivo BSL3 experiments represented in figure 4E-H, we always took along the Spike/CpG-group as positive control. We have added the additional information regarding the experimental repetitions and groups in the figure legend.

Author response:

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

Reviewer 1:

We thank Reviewer 1 for their helpful comments and hope that the changes made to the revised manuscript have addressed their points.

This study presents a novel application of the inverted encoding (i.e., decoding) approach to detect the correlates of crossmodal integration in the human EEG (electrophysiological) signal. The method is successfully applied to data from a group of 41 participants, performing a spatial localization task on auditory, visual, and audiovisual events. The analyses clearly show a behavioural superiority for audio-visual localization. Like previous studies, the results when using traditional univariate ERP analyses were inconclusive, showing once more the need for alternative, more sophisticated approaches. Instead, the principal approach of this study, harnessing the multivariate nature of the signal, captured clear signs of super-additive responses, considered by many as the hallmark of multisensory integration. Unfortunately, the manuscript lacks many important details in the descriptions of the methodology and analytical pipeline. Although some of these details can eventually be retrieved from the scripts that accompany this paper, the main text should be self-contained and sufficient to gain a clear understanding of what was done. (A list of some of these is included in the comments to the authors). Nevertheless, I believe the main weakness of this work is that the positive results obtained and reported in the results section are conditioned upon eye movements. When artifacts due to eye movements are removed, then the outcomes are no longer significant. 

Therefore, whether the authors finally achieved the aims and showed that this method of analysis is truly a reliable way to assess crossmodal integration, does not stand on firm ground. The worst-case scenario is that the results are entirely accounted for by patterns of eye movements in the different conditions. In the best-case scenario, the method might truly work, but further experiments (and/or analyses) would be required to confirm the claims in a conclusive fashion.

One first step toward this goal would be, perhaps, to facilitate the understanding of results in context by reporting both the uncorrected and corrected analyses in the main results section. Second, one could try to support the argument given in the discussion, pointing out the origin of the super-additive effects in posterior electrode sites, by also modelling frontal electrode clusters and showing they aren't informative as to the effect of interest.

We performed several additional analyses to address concerns that our main result was caused by different eye movement patterns between conditions. We re-ran our key analyses using activity exclusively from frontal electrodes, which revealed poorer decoding performance than that from posterior electrodes. If eye movements were driving the non-linear enhancement in the audiovisual condition, we would expect stronger decoding using sensors closer to the source, i.e., the extraocular muscles. We also computed the correlations between average eye position and stimulus position for each condition to evaluate whether participants made larger eye movements in the audiovisual condition, which might have contributed to better decoding results. Though we did find evidence for eye movements toward stimuli, the degree of movement did not significantly differ between conditions.

Furthermore, we note that the analysis using a stricter eye movement criterion, acknowledged in the Discussion section of the original manuscript, resulted in very similar results to the original analysis. There was significantly better decoding in the AV condition (as measured by d') than the MLE prediction, but this difference did not survive cluster correction. The most likely explanation for this is that the strict eye movement criterion combined with our conservative measure of (mass-based) cluster correction led to reduced power to detect true differences between conditions. Taken together with the additional analyses described in the revised manuscript and supplementary materials, the results show that eye movements are unlikely to account for differences between the multisensory and unisensory conditions. Instead, our decoding results likely reflect nonlinear neural integration between audio and visual sensory information.

“Any experimental design that varies stimulus location needs to consider the potential contribution of eye movements. We computed correlations between participants’ average eye position and each stimulus position between the three sensory conditions (auditory, visual and audiovisual; Figure S1) and found evidence that participants made eye movements toward stimuli. A re-analysis of the data with a very strict eye-movement criterion (i.e., removing trials with eye movements >1.875º) revealed that the super-additive enhancement in decoding accuracy no longer survived cluster correction, suggesting that our results may be impacted by the consistent motor activity of saccades towards presented stimuli. Further investigation, however, suggests this is unlikely. Though the correlations were significantly different from 0, they were not significantly different from each other. If consistent saccades to audiovisual stimuli were responsible for the nonlinear multisensory benefit we observed, we would expect to find a higher positive correlation between horizontal eye position and stimulus location in the audiovisual condition than in the auditory or visual conditions. Interestingly, eye movements corresponded more to stimulus location in the auditory and audiovisual conditions than in the visual condition, indicating that it was the presence of a sound, rather than a visual stimulus, that drove small eye movements. This could indicate that participants inadvertently moved their eyes when localising the origin of sounds. We also re-ran our analyses using the activity measured from the frontal electrodes alone (Figure S2). If the source of the nonlinear decoding accuracy in the audiovisual condition was due to muscular activity produced by eye movements, there should be better decoding accuracy from sensors closer to the source. Instead, we found that decoding accuracy of stimulus location from the frontal electrodes (peak d' = 0.08) was less than half that of decoding accuracy from the more posterior electrodes (peak d' = 0.18). These results suggest that the source of neural activity containing information about stimulus position was located over occipito-parietal areas, consistent with our topographical analyses (inset of Figure 3).” 

The univariate ERP analyses an outdated contrast, AV <> A + V to capture multisensory integration. A number of authors have pointed out the potential problem of double baseline subtraction when using this contrast, and have recommended a number of solutions, experimental and analytical. See for example: [1] and [2]. 

(1) Teder-Salejarvi, W. A., McDonald, J. J., Di Russo, F., & Hillyard, S. A. (2002). Cognitive Brain Research, 14, 106-114. 

(2) Talsma, D., & Woldorff, M. G. (2005). Journal of cognitive neuroscience, 17(7), 1098-1114.

We thank the reviewer for raising this point. Comparing ERPs across different sensory conditions requires careful analytic choices to discern genuine sensory interactions within the signal. The AV <> (A +V) contrast has often been used to detect multisensory integration, though any non-signal related activity (i.e. anticipatory waves; Taslma & Woldorff, 2005) or pre-processing manipulation (e.g. baseline subtraction; Teder-Sälejärvi et al., 2002) will be doubled in (A + V) but not in AV. Critically, we did not apply a baseline correction during preprocessing and thus our results are not at risk of double-baseline subtraction in (A + V). Additionally, we temporally jittered the presentation of our stimuli to mitigate the potential influence of consistent overlapping ERP waves (Talsma & Woldorff, 2005). 

The results section should provide the neurometric curve/s used to extract the slopes of the sensitivity plot (Figure 2B). 

We thank the reviewer for raising this point of clarification. The sensitivity plots for Figures 2B and 2C were extracted from the behavioural performance of the behavioural and EEG tasks, respectively. The sensitivity plot for Figure 2B was extracted from individual psychometric curves, whereas the d’ values for Figure 2C were calculated from the behavioural data for the EEG task. This information has been clarified in the manuscript.

“Figure 1. Behavioural performance is improved for audiovisual stimuli. A) Average accuracy of responses across participants in the behavioural session at each stimulus location for each stimulus condition, fitted to a psychometric curve. Steeper curves indicate greater sensitivity in identifying stimulus location. B) Average sensitivity across participants in the behavioural task, estimated from psychometric curves, for each stimulus condition. The red cross indicates estimated performance assuming optimal (MLE) integration of unisensory cues. C) Average behavioural sensitivity across participants in the EEG session for each stimulus condition. Error bars indicate ±1 SEM.”

The encoding model was fitted for each electrode individually; I wonder if important information contained as combinations of (individually non-significant) electrodes was then lost in this process and if the authors consider that this is relevant. 

Although the encoding model was fitted for each electrode individually for the topographic maps (Figure 4B), in all other analyses the encoding model was fitted across a selection of electrodes (see final inset of Figure 3). As this electrode set was used for all other neural analyses, our model would allow for the detection of important information contained in the neural patterns across electrodes. This information has been clarified in the manuscript.

“Thus, for all subsequent analyses we only included signals from the central-temporal, parietal-occipital, occipital and inion sensors for computing the inverse model (see final inset of Figure 2). As the model was fitted for multiple electrodes, subtle patterns of neural information contained within combinations of sensors could be detected.”

Neurobehavioral correlations could benefit from outlier rejection and the use of robust correlation statistics. 

We thank the reviewer for raising this issue. Note, however, that the correlations we report are resistant to the influence of outliers because we used Spearman’s rho1 (as opposed to Pearson’s). This information has been communicated in the manuscript.

(1) Wilcox, R.R. (2016), Comparing dependent robust correlations. British Journal of Mathematical & Statistical Psychology, 69(3), 215-224. https://doi.org/10.1111/bmsp.12069

“Neurobehavioural correlations. As behavioural and neural data violated assumptions of normality, we calculated rank-order correlations (Spearman’s rho) between the average decoding sensitivity for each participant from 150-250 ms poststimulus onset and behavioural performance on the EEG task. As Spearman’s rho is resistant to outliers (Wilcox, 2016), we did not perform outlier rejection.”

“Wilcox, R.R. (2016), Comparing dependent robust correlations. British Journal of Mathematical & Statistical Psychology, 69(3), 215-224. https://doi.org/10.1111/bmsp.12069”

Many details that are important for the reader to evaluate the evidence and to understand the methods and analyses aren't given; this is a non-exhaustive list:  

We thank the reviewer for highlighting these missing details. We have updated the manuscript where necessary to ensure the methods and analyses are fully detailed and replicable.

- specific parameters of the stimuli and performance levels. Just saying "similarly difficult" or "marginally higher volume" is not enough to understand exactly what was done.  

“The perceived source location of auditory stimuli was manipulated via changes to interaural level and timing (Whitworth & Jeffress, 1961; Wightman & Kistler, 1992). The precise timing of when each speaker delivered an auditory stimulus was calculated from the following formula:

where x and z are the horizontal and forward distances in metres between the ears and the source of the sound on the display, respectively, r is the head radius, and s is the speed of sound. We used a constant approximate head radius of 8 cm for all participants. r was added to x for the left speaker and subtracted for the right speaker to produce the interaural time difference. For ±15° source locations, interaural timing difference was 1.7 ms. To simulate the decrease in sound intensity as a function of distance, we calculated interaural level differences for the left and right speakers by dividing the sounds by the left and right distance vectors. Finally, we resampled the sound using linear interpolation based on the calculations of the interaural level and timing differences. This process was used to calculate the soundwaves played by the left and right speakers for each of the possible stimulus locations on the display. The maximum interaural level difference between speakers was 0.14 A for ±15° auditory locations, and 0.07 A for ±7.5°.”

- where are stimulus parameters adjusted individually or as a group? Which method was followed?  

To clarify, stimulus parameters (frequency, size, luminance, volume, location, etc.) were manipulated throughout pilot testing only. Parameters were adjusted to achieve similar pilot behavioural results between the auditory and visual conditions. For the experiment proper, parameters remained constant for both tasks and were the same for all participants.

“During pilot testing, stimulus features (size, luminance, volume, frequency etc.) were manipulated to make visual and auditory stimuli similarly difficult to spatially localize. These values were held constant in the main experiment.”

- specify which response buttons were used.

“Participants were presented with two consecutive stimuli and tasked with indicating, via button press, whether the first (‘1’ number-pad key) or second (‘2’ number-pad key) interval contained the more leftward stimulus.”

“At the end of each sequence, participants were tasked with indicating, via button press, whether more presentations appeared on the right (‘right’ arrow key) or the left (‘left’ arrow key) of the display.”

- no information is given as to how many trials per condition remained on average, for analysis.  

The average number of remaining trials per condition after eye-movement analysis is now included in the Methods section of the revised manuscript.

“We removed trials with substantial eye movements (>3.75 away from fixation) from the analyses. After the removal of eye movements, on average 2365 (SD \= 56.94), 2346 (SD \= 152.87) and 2350 (SD \= 132.47) trials remained for auditory, visual and audiovisual conditions, respectively, from the original 2400 per condition.”

- no information is given on the specifics of participant exclusion criteria. (even if the attrition rate was surprisingly high, for such an easy task).  

The behavioural session also served as a screening task. Although the task instructions were straightforward, perceptual discrimination was not easy due to the ambiguity of the stimuli. Auditory localization is not very precise, and the visual stimuli were brief, dim, and diffuse. The behavioural results reflect the difficulty of the task. Attrition rate was high as participants who scored below 60% correct in any condition were deemed unable to accurately perform the task, were not invited to complete the subsequent EEG session, and omitted from the analyses. We have included the specific criteria in the manuscript.

“Participants were first required to complete a behavioural session with above 60% accuracy in all conditions to qualify for the EEG session (see Behavioural session for details).”

- EEG pre-processing: what filter was used? How was artifact rejection done? (no parameters are reported); How were bad channels interpolated?  

We used a 0.25 Hz high-pass filter to remove baseline drifts, but no low-pass filter. In line with recent studies on the undesirable influence of EEG preprocessing on ERPs1, we opted to avoid channel interpolation and artifact rejection. This was erroneously reported in the manuscript and has now been clarified. For the sake of clarity, here we demonstrate that a reanalysis of data using channel interpolation and artifact rejection returned the same pattern of results. 

(1) Delorme, A. (2023). EEG is better left alone. Scientific Reports, 13, 2372. https://doi.org/10.1038/s41598-023-27528-0

- specific electrode locations must be given or shown in a plot (just "primarily represented in posterior electrodes" is not sufficiently informative).  

A diagram of the electrodes used in all analyses is included within Figure 3, and we have drawn readers’ attention to this in the revised manuscript.

“Thus, for all subsequent analyses we only included signals from the central-temporal, parietal-occipital, occipital and inion sensors for computing the inverse model (see final inset of Figure 2).” 

- ERP analysis: which channels were used? What is the specific cluster correction method?

We used a conservative mass-based cluster correction from Pernet et al. (2015) - this information has been clarified in the manuscript.

“A conservative mass-based cluster correction was applied to account for spurious differences across time (Pernet et al., 2015).” 

“Pernet, C. R., Latinus, M., Nichols, T. E., & Rousselet, G. A. (2015). Cluster-based computational methods for mass univariate analyses of event-related brain potentials/fields: A simulation study. Journal of Neuroscience Methods, 250, 85-93. https://doi.org/https://doi.org/10.1016/j.jneumeth.2014.08.003” 

- results: descriptive stats on performance must be given (instead of saying "participants performed well").  

The mean and standard deviation of participants’ performance for each condition in the behavioural and EEG experiments are now explicitly mentioned in the manuscript.

“A quantification of the behavioural sensitivity (i.e., steepness of the curves) revealed significantly higher sensitivity for the audiovisual stimuli (M = .04, SD = .02) than for the auditory stimuli alone (M = .03, SD = .01; Z = -3.09, p = .002), and than for the visual stimuli alone (M = .02, SD = .01; Z = -5.28, p = 1.288e-7; Figure 1B). Sensitivity for auditory stimuli was also significantly higher than sensitivity for visual stimuli (Z = 2.02, p = .044).” 

“We found a similar pattern of results to those in the behavioural session; sensitivity for audiovisual stimuli (M = .85, SD = .33) was significantly higher than for auditory (M = .69, SD = .41; Z = -2.27, p = .023) and visual stimuli alone (M = .61, SD = .29; Z = -3.52, p = 4.345e-4), but not significantly different from the MLE prediction (Z = -1.07, p = .285).” 

- sensitivity in the behavioural and EEG sessions is said to be different, but no comparison is given. It is not even the same stimulus set across the two tasks...  

This relationship was noted as a potential explanation for the higher sensitivities obtained in the EEG task, and was not intended to stand up to statistical scrutiny. We agree it makes little sense to compare statistically between the EEG and behavioural results as they were obtained from different tasks. We would like to clarify, however, that the stimuli used in the two tasks were the same, with the exception that in the EEG task the stimuli were presented from 5 locations versus 8 in the behavioural task. To avoid potential confusion, we have removed the offending sentence from the manuscript:

Reviewer 2:

Their measure of neural responses is derived from the decoder responses, and this takes account of the reliability of the sensory representations - the d' statistics - which is an excellent thing. It also means if I understand their analysis correctly (it could bear clarifying - see below), that they can generate from it a prediction of the performance expected if an optimal decision is made combining the neural signals from the individual modalities. I believe this is the familiar root sum of squares d' calculation (or very similar). Their decoding of the audiovisual responses comfortably exceeds this prediction and forms part of the evidence for their claims. 

Yet, superadditivity - including that in evidence in the principle of inverse effectiveness more typically quantifies the excess over the sum of proportions correct in each modality. Their MLE d' statistic can already predict this form of superadditivity. Therefore, the superadditivity they report here is not the same form of superadditivity that is usually referred to in behavioural studies. It is in fact a stiffer definition. What their analysis tests is that decoding performance exceeds what would be expected from an optimally weighted linear integration of the unisensory information. As this is not the common definition it is difficult to relate to behavioral superadditivity reported in much literature (of percentage correct). This distinction is not at all clear from the manuscript. 

But the real puzzle is here: The behavioural data or this task do not exceed the optimal statistical decision predicted by signal detection theory (the MLE d'). Yet, the EEG data would suggest that the neural processing is exceeding it. So why, if the neural processing is there to yield better performance is it not reflected in the behaviour? I cannot explain this, but it strikes me that the behaviour and neural signals are for some reason not reflecting the same processing. 

Be explicit and discuss this mismatch they observe between behaviour and neural responses. 

Thank you, we agree that it is worth expanding on the observed disconnect between MSI in behaviour and neural signals. We have included an additional paragraph in the Discussion of the revised manuscript. Despite the mismatch, we believe the behavioural and neural responses still reflect the same underlying processing, but at different levels of sensitivity. The behavioural result likely reflects a coarse down-sampling of the precision in location representation, and thus less likely to reflect subtle MSI enhancements.

“An interesting aspect of our results is the apparent mismatch between the behavioural and neural responses. While the behavioural results meet the optimal statistical threshold predicted by MLE, the decoding analyses suggest that the neural response exceeds it. Though non-linear neural responses and statistically optimal behavioural responses are reliable phenomena in multisensory integration (Alais & Burr, 2004; Ernst & Banks, 2002; Stanford & Stein, 2007), the question remains – if neural super-additivity exists to improve behavioural performance, why is it not reflected in behavioural responses? A possible explanation for this neurobehavioural discrepancy is the large difference in timing between sensory processing and behavioural responses. A motor response would typically occur some time after the neural response to a sensory stimulus (e.g., 70-200 ms), with subsequent neural processes between perception and action that introduce noise (Heekeren et al., 2008) and may obscure super-additive perceptual sensitivity. In the current experiment, participants reported either the distribution of 20 serially presented stimuli (EEG session) or compared the positions of two stimuli (behavioural session), whereas the decoder attempts to recover the location of every presented stimulus. While stimulus location could be represented with higher fidelity in multisensory relative to unisensory conditions, this would not necessarily result in better performance on a binary behavioural task in which multiple temporally separated stimuli are compared. One must also consider the inherent differences in how super-additivity is measured at the neural and behavioural levels. Neural super-additivity should manifest in responses to each individual stimulus. In contrast, behavioural super-additivity is often reported as proportion correct, which can only emerge between conditions after being averaged across multiple trials. The former is a biological phenomenon, while the latter is an analytical construct. In our experiment, we recorded neural responses for every presentation of a stimulus, but behavioural responses were only obtained after multiple stimulus presentations. Thus, the failure to find super-additivity in behavioural responses might be due to their operationalisation, with between-condition comparisons lacking sufficient sensitivity to detect super-additive sensory improvements. Future work should focus on experimental designs that can reveal super-additive responses in behaviour.”

Re-work the introduction to explain more clearly the relationship between the behavioural superadditivities they review, the MLE model, and the superadditivity it actually tests. 

We agree it is worth discussing how super-additivity is operationalised across neural and behavioural measures. However, we do not believe the behavioural studies we reviewed claimed super-additive behavioural enhancements. While MLE is often used as a behavioural marker of successful integration, it is not necessarily used as evidence for super-additivity within the behavioural response, as it relies on linear operations. 

“It is important to consider the differences in how super-additivity is classified between neural and behavioural measures. At the level of single neurons, superadditivity is defined as a non-linear response enhancement, with the multisensory response exceeding the sum of the unisensory responses. In behaviour, meanwhile, it has been observed that the performance improvement from combining two senses is close to what is expected from optimal integration of information across the senses (Alais & Burr, 2004; Stanford & Stein, 2007). Critically, behavioural enhancement of this kind does not require non-linearity in the neural response, but can arise from a reliability-weighted average of sensory information. In short, behavioural performance that conforms to MLE is not necessarily indicative of neural super-additivity, and the MLE model can be considered a linear baseline for multisensory integration.”

Regarding the auditory stimulus, this reviewer notes that interaural time differences are unlikely to survive free field presentation.

Despite the free field presentation, in both the pilot test and the study proper participants were able to localize auditory stimuli significantly above chance. 

"However, other studies have found super-additive enhancements to the amplitude of sensory event-related potentials (ERPs) for audiovisual stimuli (Molholm et al., 2002; Talsma et al., 2007), especially when considering the influence of stimulus intensity (Senkowski et al., 2011)." - this makes it obvious that there are some studies which show superadditivity. It would have been good to provide a little more depth here - as to what distinguished those studies that reported positive effects from those that did not.

We have provided further detail on how super-additivity appears to manifest in neural measures.

“In EEG, meanwhile, the evoked response to an audiovisual stimulus typically conforms to a sub-additive principle (Cappe et al., 2010; Fort et al., 2002; Giard & Peronnet, 1999; Murray et al., 2016; Puce et al., 2007; Stekelenburg & Vroomen, 2007; Teder- Sälejärvi et al., 2002; Vroomen & Stekelenburg, 2010). However, when the principle of inverse effectiveness is considered and relatively weak stimuli are presented together, there has been some evidence for super-additive responses (Senkowski et al., 2011).”

“While behavioural outcomes for multisensory stimuli can be predicted by MLE, and single neuron responses follow the principles of inverse effectiveness and super- additivity, among others (Rideaux et al., 2021), how audiovisual super-additivity manifests within populations of neurons is comparatively unclear given the mixed findings from relevant fMRI and EEG studies. This uncertainty may be due to biophysical limitations of human neuroimaging techniques, but it may also be related to the analytic approaches used to study these recordings. For instance, superadditive responses to audiovisual stimuli in EEG studies are often reported from very small electrode clusters (Molholm et al., 2002; Senkowski et al., 2011; Talsma et al., 2007), suggesting that neural super-additivity in humans may be highly specific. However, information encoded by the brain can be represented as increased activity in some areas, accompanied by decreased activity in others, so simplifying complex neural responses to the average rise and fall of activity in specific sensors may obscure relevant multivariate patterns of activity evoked by a stimulus.”

P9. "(25-75 W, 6 Ω)." This is not important, but it is a strange way to cite the power handling of a loudspeaker. 

“The loudspeakers had a power handling capacity of 25-75 W and a nominal impedance of 6 Ω.” 

I am struggling to understand the auditory stimulus: 

"Auditory stimuli were 100 ms clicks". Is this a 100-ms long train of clicks? A single pulse which is 100ms long would not sound like a click, but two clicks once filtered by the loudspeaker. Perhaps they mean 100us. 

"..with a flat 850 Hz tone embedded within a decay envelope". Does this mean the tone is gated - i.e. turns on and off slowly? Or is it constant?

We thank the reviewer for catching this. ‘Click’ may not be the most apt way of defining the auditory stimulus. It was a 100 ms square wave tone with decay, i.e., with an onset at maximal volume before fading gradually. Given that the length of the stimulus was 100 ms, the decay occurs quickly and provides a more ‘click-like’ percept than a pure tone. We have provided a representation of the sound below for further clarification. This represents the amplitude from the L and R speakers for maximally-left and maximally-right stimuli. We have added this clarification in the revised manuscript. 

Author response image 1.

“Auditory stimuli were 100 ms, 850 Hz tones with a decay function (sample rate = 44, 100 Hz; volume = 60 dBA SPL, as measured at the ears).”

P10. "Stimulus modality was either auditory, visual, or audiovisual. Trials were blocked with short (~2 min) breaks between conditions".

Presumably the blocks were randomised across participants.

Condition order was not randomised across participants, but counterbalanced. This has been clarified in the manuscript.

“Stimulus modality was auditory, visual or audiovisual, presented in separate blocks with short breaks (~2 min) between conditions (see Figure 6A for an example trial). The order of conditions was counterbalanced across participants.” 

P15. Feels like there is a step not described here: "The d' of the auditory and visual conditions can be used to estimate the predicted 'optimal' sensitivity of audiovisual signals as calculated through MLE." Do they mean sqrt[ (d'A)^2 + (d'V)^2] ? If it is so simple then it may as well be made explicit here. A quick calculation from eyeballing Figures 2B and 2C suggests this is the case.

We thank the reviewer for raising this point of clarification. Yes, the ‘optimal’ audiovisual sensitivity was calculated as the hypotenuse of the auditory and visual sensitivities. This calculation has been made explicit in the revised manuscript.

The d’ from the auditory and visual conditions can be used to estimate the predicted ‘optimal’ sensitivity to audiovisual signals as calculated through the following formula:

"The perceived source location of auditory stimuli was manipulated via changes to interaural intensity and timing (Whitworth & Jeffress, 1961; Wightman & Kistler, 1992)." The stimuli were delivered by a pair of loudspeakers, and the incident sound at each ear would be a product of both speakers. And - if there were a time delay between the two speakers, then both ears could potentially receive separate pulses one after the other at different delays. Did they record this audio stimulus with manikin? If not, it would be very difficult to know what it was at the ears. I don't doubt that if they altered the relative volume of the loudspeakers then some directionality would be perceived but I cannot see how the interaural level and timing differences could be matched - as if the sound were from a single source. I doubt that this invalidates their results, but to present this as if it provided matched spatial and timing cues is wrong, and I cannot work out how they can attribute an azimuthal location to the sound. For replication purposes, it would be useful to know how far apart the loudspeakers were and what the timing and level differences actually were.

The behavioural tasks each had evenly distributed ‘source locations’ on the horizontal azimuth of the computer display (8 for the behavioural session, 5 for the EEG session). We manipulated the perceived location of auditory stimuli through interaural time delays and interaural level differences. By first measuring the forward (z) and horizontal (x) distance of each source location to each ear, the method worked by calculating what the time-course of a sound wave should be at the location of the ear given the sound wave at the source. Then, for each source location, we can calculate the time delay between speakers given the vectors of x and z, the speed of sound and the width of the head.  As the intensity of sound drops inversely with the square of the distance, we can divide the sound wave by the distance for each source location to provide the interaural level difference. Though we did not record the auditory stimulus with a manikin, our behavioural analyses show that participants were able to detect the directions of auditory stimuli from our manipulations, even to a degree that significantly exceeded the localisation accuracy for visual stimuli (for the behavioural session task). This information has been clarified in the manuscript.

“Auditory stimuli were played through two loudspeakers placed either side of the display (80 cm apart for the behavioural session, 58 cm apart for the EEG session).” 

“The perceived source location of auditory stimuli was manipulated via changes to interaural level and timing (Whitworth & Jeffress, 1961; Wightman & Kistler, 1992). The precise timing of when each speaker delivered an auditory stimulus was calculated from the following formula:

where x and z are the horizontal and forward distances in metres between the ears and the source of the sound on the display, respectively, r is the head radius, and s is the speed of sound. We used a constant approximate head radius of 8 cm for all participants. r was added to x for the left speaker and subtracted for the right speaker to produce the interaural time difference. For ±15° source locations, interaural timing difference was 1.7 ms. To simulate the decrease in sound intensity as a function of distance, we calculated interaural level differences for the left and right speakers by dividing the sounds by the left and right distance vectors. Finally, we resampled the sound using linear interpolation based on the calculations of the interaural level and timing differences. This process was used to calculate the soundwaves played by the left and right speakers for each of the possible stimulus locations on the display. The maximum interaural level difference between speakers was 0.14 A for ±15° auditory locations, and 0.07 A for ±7.5°.

I am confused about this statement: "A quantification of the behavioural sensitivity (i.e., steepness of the curves) revealed significantly greater sensitivity for the audiovisual stimuli than for the auditory stimuli alone (Z = -3.09, p = .002)," It is not clear from the methods how they attributed sound source angle to the sounds. Conceivably they know the angle of the loudspeakers, and this would provide an outer bound on the perceived location of the sound for extreme interaural level differences (although free field interaural timing cues can create a wider sound field). 

Our analysis of behavioural sensitivity was dependent on the set ‘source locations’ that were used to calculate the position of auditory and audiovisual stimuli.  In the behavioural task, participants judged the position of the target stimulus relative to a central stimulus. Thus, for each source location, we recorded how often participants correctly discriminated between presentations. The quoted analysis acknowledges that participants were more sensitive to audiovisual stimuli than auditory stimuli in the context of this task. A full explanation of how source location was implemented for auditory stimuli has been clarified in the manuscript. 

It would be very nice to see some of the "channel" activity - to get a feel for the representation used by the decoder. 

We have included responses for the five channels as a Supplemental Figure.

Figure 6 appears to show that there is some agreement between behaviour and neural responses - for the audiovisual case alone. The positive correlation of behavioural and decoding sensitivity appears to be driven by one outlier - who could not perform the audiovisual task (and indeed presumably any of them). Furthermore, if we were simply Bonferonni correct for the three comparisons, this would become non-significant. It is also puzzling why the unisensory behaviour and EEG do not correlate - which seems to again suggest a poor correspondence between them. Opposite to the claim made.

We understand the reviewer’s concern here. We would like to note, however, that each correlation used unique data sets – that is, the behavioural and neural data for each separate condition. In this case, we believe a Bonferroni correction for multiple comparisons is too conservative, as no data set was compared more than once. Neither the behavioural nor the neural data were normally distributed, and both contained outliers. Rather than reduce power through outlier rejection, we opted to test correlations using Spearman’s rho, which is resistant to outliers1. It is also worth noting that, without outlier rejection, the audiovisual correlation (p \= .003) would survive a Bonferroni correction for 3 comparisons. The nonsignificant correlation in the auditory and visual conditions might be due to the weaker responses elicited by unisensory stimuli, with the reduced signal-to-noise ratio obscuring potential correlations. Audiovisual stimuli elicited more precise responses both behaviourally and neurally, increasing the power to detect a correlation. 

(1) Wilcox, R.R. (2016), Comparing dependent robust correlations. British Journal of Mathematical & Statistical Psychology, 69(3), 215-224. https://doi.org/10.1111/bmsp.12069

“We also found a significant positive correlation between participants’ behavioural judgements in the EEG session and decoding sensitivity for audiovisual stimuli. This result suggests that participants who were better at identifying stimulus location also had more reliably distinct patterns of neural activity. The lack of neurobehavioural correlation in the unisensory conditions might suggest a poor correspondence between the different tasks, perhaps indicative of the differences between behavioural and neural measures explained previously. However, multisensory stimuli have consistently been found to elicit stronger neural responses than unisensory stimuli (Meredith & Stein, 1983; Puce et al., 2007; Senkowski et al., 2011; Vroomen & Stekelenburg, 2010), which has been associated with behavioural performance (Frens & Van Opstal, 1998; Wang et al., 2008). Thus, the weaker signalto-noise ratio in unisensory conditions may prevent correlations from being detected.”

Further changes:

(1)   To improve clarity, we shifted the Methods section to after the Discussion. This change included updating the figure numbers to match the new order (Figure 1 becomes Figure 6, Figure 2 becomes Figure 1, and so on).

(2)   We also resolved an error on Figure 2 (previously Figure 3). The final graph (Difference between AV and A + V) displayed incorrect values on the Y axis.

This has now been remedied.

Author Response

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

We would like to thank the editor and all the reviewers for their time and thoughtful consideration of our manuscript. We appreciate the valuable comments. Our provisional response to the “public review” has been published and now we have corrected factual errors and enhanced the clarity of writings based on the “recommendations for the authors.” We believe these corrections will improve the quality and accuracy of our manuscript.

Specific responses to the reviewers' recommendations for the authors are as follows:

Reviewer #1 (Recommendations For The Authors):

1) Is the Slack current amplitude dependent on the Nav subtype? Differences in Slack current amplitude might explain the sensitization of Slack to quinidine.

We appreciate the reviewer for raising this point. We examined Slack current amplitudes upon co-expression of Slack with specific NaV subtypes in HEK293 cells. The results have shown that there are no significant differences in Slack current amplitudes upon co-expression of Slack with different NaV channel subtypes (Author response image 1), suggesting whole-cell Slack current amplitudes cannot explain the varied ability of NaV subtypes to sensitize Slack to quinidine blockade.

Author response image 1.

The amplitudes of Slack currents upon co-expression of Slack with specific NaV subtypes in HEK293 cells. ns, p > 0.05, one-way ANOVA followed by Bonferroni’s post hoc test.

2) Is the open probability changed by the presence of Nav1.6 and/or by the other Nav subtypes? Changes in open probability might explain the Nav1.6 induced sensitization of Slack to quinidine block.

We appreciate the reviewer for raising this point. To investigate the effect of different NaV channel subtypes on Slack open probability, we will perform the single-channel recordings in future studies.

3) Could the authors elaborate more on the coupling between INaT mediated sensitization of Slack to block by quinidine and the Nav1.6 N-and C-tail induced sensitization?

We appreciate the reviewer for raising this point. We fully agree the importance of investigating the detailed mechanism underlying the sensitization of Slack to quinidine blockade. To address the questions, we plan to employ structural biological methods, such as cryo-electron microscopy (cryo-EM).

4) Line 85: The authors use an outdated nomenclature of AMPAR subtypes. I would suggest changing to GluA1, GluA2, GluA3 and GluA4.

We appreciate the reviewer’s suggestion. We have changed the term “GluR” to “GluA” in the revised manuscript.

The authors do not explain the rationale by using the different homomeric AMPAR subtypes. Most often the AMPARs express as heteromeric receptors decorated by auxiliary subunits. Also, is the GluA2 the edited version?

We thank the reviewer for raising this point. While AMPARs are often expressed as heteromeric receptors with auxiliary subunits, we focused on the homomeric AMPAR subtypes for initial screening. Through our investigation, we found no significant effects on sensitizing Slack to quinidine blockade. Additionally, the GluA2 used in our study is unedited.

5) Line 144: I expect a reduction in current amplitude caused by blocking INaT and INaP is tested at +100mV?

We thank the reviewer for raising this point. The reduction in current amplitude was indeed tested at +100 mV and we have included this information in the revised manuscript.

6) Line 157 and line 162: Reference to Supplementary table S3 should be Table S2.

We thank the reviewer for pointing this out. The reference to "Table S3" has been corrected to "Table S2" in the revised manuscript.

7) How many times did the authors repeat the co-immunoprecipitation? Some of the bands are very weak, and repeats are necessary for all blots.

We thank the reviewer for raising this concern. We performed the co-immunoprecipitation experiments three times independently.

8) Line 288: The authors are showing the chimeric construct in Figures 7A and B but are referring to the full length Nav1.6 in the main text line 288.

We apologize for the confusion. We have clarified in the revised manuscript that we used NaV1.5/6NC in our study.

9) Figure 1 line 23: 1 uM quinidine must be 30 uM quinidine?

We thank the reviewer for catching this error. We have corrected the concentration value in the caption of Figure 1 from "1 μΜ" to "30 μΜ" in the revised manuscript.

10) Figure 2 line 53: I expect IC50 is measured at +100mV? Same question for line 60 in same figure text.

We thank the reviewer for pointing this out. We have now included this information in the revised manuscript.

11) Figure 4B color coding is confusing.

We apologize for the confusion. We would like to clarify that Fig. 4B illustrates the domain architecture of the human NaV channel pore-forming α subunit, and we have changed the color from dark blue to black in the revised figure.

12) Figure S6: Text for figure S6E and S6F has been swapped (line 96 to 106).

We thank the reviewer for raising this point. We have rectified the swapped captions for Fig. S6E and Fig. S6F in the revised manuscript.

13) Methods section line 652: Kainite acid should be changed to kainic acid

We thank the reviewer for catching this typo. The term “kainite acid” has been corrected to “kainic acid” in the revised manuscript.

Reviewer #2 (Recommendations For The Authors):

1) Discuss limitations about the use of non-neuronal cells or cultured primary neurons rather than a more intact system.

We thank the reviewer for raising this point. We have discussed the limitations about the use of non-neuronal cells or cultured primary neurons rather than a more intact system (line 344 to line 348).

2) Riluzole is not a selective drug, so the limitations of this drug should be discussed.

We thank the reviewer for raising this point. We have discussed the limitations of riluzole in the revised manuscript (line 360 to line 364).

3) Remove the term in vivo.

We thank the reviewer for raising this point. In our experiments, although we did not conduct experiments directly in living organisms, our results demonstrated the coimmunoprecipitation of NaV1.6 with Slack in homogenates from mouse cortical and hippocampal tissues (Fig. 3C). This result may support that the interaction between Slack and NaV1.6 occurs in vivo.

4) Figure 1

①C Why does Nav1.2 have a small inward current before the large inward current in the inset? The slope of the rising phase of the larger sodium current seems greater than Nav1.6 or Nav1.5. Was this examined?

We apologize for the confusion. We would like to clarify that the small inward current can be attributed to the current of membrane capacitance (slow capacitance or C-slow). The larger inward current is mediated by NaV1.2. Additionally, we did not compare the slope of the rising phase of NaV subtypes sodium currents but primarily focused on the current amplitudes.

②D-E

For Nav1.5 the sodium current is very large compared to Nav1.6. Is it possible the greater effect of quinidine for Nav1.6 is due to the lesser sodium current of Nav1.6?

We thank the reviewer for raising this point. We would like to clarify that our results indicate that transient sodium currents contribute to the sensitization of Slack to quinidine blockade (Fig. 2C,E). Therefore, it is unlikely that the greater effect observed for NaV1.6 in sensitizing Slack is due to its lower sodium currents.

③The differences between WT and KO in G -H are hard to appreciate. Could quantification be shown? The text uses words like "block" but this is not clear from the figure. It seems that the replacement of Na+ with Li+ did not block the outward current or effect of quinidine.

We apologize for the confusion. We would like to clarify the methods used in this experiment. The lithium ion (Li+) is a much weaker activator of sodium-activated potassium channel Slack than sodium ion (Na+)1,2.

1. Zhang Z, Rosenhouse-Dantsker A, Tang QY, Noskov S, Logothetis DE. The RCK2 domain uses a coordination site present in Kir channels to confer sodium sensitivity to Slo2.2 channels. J Neurosci. Jun 2 2010;30(22):7554-62. doi:10.1523/JNEUROSCI.0525-10.2010

2. Kaczmarek LK. Slack, Slick and Sodium-Activated Potassium Channels. ISRN Neurosci. Apr 18 2013;2013(2013)doi:10.1155/2013/354262

Therefore, we replaced Na+ with Li+ in the bath solution to measure the current amplitudes of sodium-activated potassium currents (IKNa)3.

1. Budelli G, Hage TA, Wei A, et al. Na+-activated K+ channels express a large delayed outward current in neurons during normal physiology. Nat Neurosci. Jun 2009;12(6):745-50. doi:10.1038/nn.2313

The following equation was used for quantification:

Furthermore, the remaining IKNa after application of 3 μM quinidine in the bath solution was measured as the following:

The quantification results were presented in Fig. 1K. The term "block" used in the text referred to the inhibitory effect of quinidine on IKNa.

④In K, for the WT, why is the effect of quinidine only striking for the largest currents?

We thank the reviewer for raising this point. After conducting an analysis, we found no correlation between the inhibitory effect of quinidine and the amplitudes of baseline IKNa in WT neurons (p = 0.6294) (Author response image 2). Therefore, the effect of quinidine is not solely limited to targeting the larger currents.

Author response image 2.

The correlation between the inhibitory effect of quinidine and the amplitudes of baseline IKNa in WT neurons (data from manuscript Fig. 1K). r = 0.1555, p=0.6294, Pearson correlation analysis.

5) Figure 2

①A. The argument could be better made if the same concentration of quinidine were used for Slack and Slack + Nav1.6. It is recognized a greater sensitivity to quinidine is to be shown but as presented the figure is a bit confusing.

We apologize for the confusion. We would like to clarify that the presented concentrations of quinidine were chosen to be near the IC50 values for Slack and Slack+NaV1.6.

②C. Can the authors add the effect of quinidine to the condition where the prepulse potential was - 90?

We apologize for the confusion. We would like to clarify that the condition of prepulse potential at -90 mV is the same as the condition in Fig. 1. We only changed one experiment condition where the prepulse potential was changed to -40 mV from -90 mV.

6) Figure 3.

①line 80 should be coronal not coronary

We thank the reviewer for catching this error. We have corrected the term “coronary” to “coronal” in the caption of Figure 3.

②A. Clarify these 6 panels.

We thank the reviewer for raising this point. We have clarified the captions of Fig. 3A in the revised manuscript.

③Please enlarge fonts in D.

We thank the reviewer’s suggestion. We’ve enlarged the fonts in Fig. 3D in the revised manuscript.

④F. The variances should be checked with a test to determine if they are significantly different because they look different - if so, data can be transformed and if transformed data have variances that are equivalent a t-test can be used on the transformed data. Otherwise, Mann-Whitney should be used.

We thank the reviewer for pointing this out. We have reanalyzed the data in Fig. 3F using Mann Whitney test after identifying the different variances in the two groups.

7) Figure 7. The images need more clarity. They are very hard to see. Text is also hard to see.

We apologize for the lack of clarity in the images and text. we would like to provide a concise summary of the key findings shown in this figure.

Figure 7 illustrates an innovative intervention for treating SlackG269S-induced seizures in mice by disrupting the Slack-NaV1.6 interaction. Our results showed that blocking NaV1.6-mediated sodium influx significantly reduced Slack current amplitudes (Fig. 2D,G), suggesting that the Slack-NaV1.6 interaction contributes to the current amplitudes of epilepsy-related Slack mutant variants, aggravating the gain-of-function phenotype. Additionally, Slack’s C-terminus is involved in the Slack-NaV1.6 interaction (Fig. 5D). We assumed that overexpressing Slack’s C-terminus can disrupt the Slack-NaV1.6 interaction (compete with Slack) and thereby encounter the current amplitudes of epilepsy-related Slack mutant variants.

In HEK293 cells, overexpression of Slack’s C-terminus indeed significantly reduced the current amplitudes of epilepsy-related SlackG288S and SlackR398Q upon co-expression with NaV1.5/6NC (Fig. 7A,B). Subsequently, we evaluated this intervention in an in vivo epilepsy model by introducing the Slack G269S variant into C57BL/6N mice using AAV injection, mimicking the human Slack mutation G288S that we previously identified (Fig. 7C-G).

②It is not clear how data were obtained because injection of kainic acid does not lead to a convulsive seizure every 10 min for several hours, which is what appears to be shown. Individual seizures are just at the beginning and then they merge at the start of status epilepticus. After the onset of status epilepticus the animals twitch, have varied movements, sometime rear and fall, but there is not a return to normal behavior. Therefore one can not call them individual seizures. In some strains of mice, however, individual convulsive seizures do occur (even if the EEG shows status epilepticus is occurring) but there are rarely more than 5 over several hours and the graph has many more. Please explain.

We apologize for the confusion. Regarding the data acquisition in relation to kainic acid injection, we initiated the timing following intraperitoneal injection of kainic acid and recorded the seizure scores of per mouse at ten-minute intervals, following the methodology described in previous studies4.

1. Huang Z, Walker MC, Shah MM. Loss of dendritic HCN1 subunits enhances cortical excitability and epileptogenesis. J Neurosci. Sep 2 2009;29(35):10979-88. doi:10.1523/JNEUROSCI.1531-09.2009

The seizure scores were determined using a modified Racine, Pinal, and Rovner scale5,6: (1) Facial movements; (2) head nodding; (3) forelimb clonus; (4) dorsal extension (rearing); (5) Loss of balance and falling; (6) Repeated rearing and failing; (7) Violent jumping and running; (8) Stage 7 with periods of tonus; (9) Dead.

1. Pinel JP, Rovner LI. Electrode placement and kindling-induced experimental epilepsy. Exp Neurol. Jan 15 1978;58(2):335-46. doi:10.1016/0014-4886(78)90145-0

2. Racine RJ. Modification of seizure activity by electrical stimulation. II. Motor seizure. Electroencephalogr Clin Neurophysiol. Mar 1972;32(3):281-94. doi:10.1016/0013- 4694(72)90177-0

8) The graphical abstract is quite complicated and somewhat hard to follow. Please simplify and clarify. One aspect of the abstract to clarify is the direction of what is first and second and third (etc.) because arrows point to many directions.

We thank the review for raising this point. In the revised manuscript, we have included numbering of three components within the graphical abstract:

1. Pathological phenotype: Increased Slack currents.

2. Two types of interventions:

2a. Disruption of the Slack-NaV1.6 interaction.

2b. NaV1.6-mediated sensitization of Slack to quinidine blockade.

1. Therapeutic effects: Reduced Slack currents.

Reviewer #3 (Recommendations For The Authors):

1) A reference to homozygous knockout is made in the abstract; however, only heterozygous mice are mentioned in the methods section. The genotype of the mice needs to be made clear in the manuscript. Furthermore, at what age were these mice used in the study. Since homozygous knockout of NaV1.6 is lethal at a very young age (<4 wks), it would be important to clarify that point as well.

We thank the reviewer for pointing this out. In the revised manuscript, we have included information about the source of the primary cortical neurons used in our study. These neurons were obtained from postnatal homozygous NaV1.6 knockout C3HeB/FeJ mice and their wild-type littermate controls.

2) Coimmunoprecipitation studies in Fig. 3C are not convincing. There appears to be a signal in the control lane. Furthermore, it appears that brightness levels were adjusted of that image, thereby removing completely the background.

We thank the reviewer for pointing this out. We have replaced Fig. 3C with an unadjusted version in the revised manuscript.

3) In Fig. 1B, the authors indicate that 30 microM of quinidine was used, while the corresponding figure legend suggest that 1 microM. Please clarify.

We apologize for this error. We have corrected the concentration value in the caption of Figure 1 from "1 μΜ" to "30 μΜ" in the revised manuscript.

4) How long were the cells exposed to quinidine before the functional measurement were performed?

We thank the reviewer for pointing this out. The cells were exposed to the bath solution with quinidine for about one minute before applying step pulses.

5) In Fig. 6B-D, it is not clear to what extent co-expression of Slack mutants and NaV1.6 increases sodium-activated potassium current.

We thank the reviewer for pointing this out. We notice that the current amplitudes of Slack mutants exhibit a considerable degree of variation, ranging from less than 1 nA to over 20 nA (n = 5-8). To accurately measure the effects of NaV1.6 on increasing current amplitudes of Slack mutants, we plan to apply tetrodotoxin in the bath solution to block NaV1.6 sodium currents upon coexpression of Slack mutants with NaV1.6.

6) In Fig.7A and B, it appears that some recordings had no sodium-activated potassium currents. Why were these included in analysis? How was transfection efficacy assessed?

We apologize for the confusion. We would like to clarify that all recordings included in analysis indeed exhibited outward sodium-activated potassium currents. The current density data in Fig. 7A-B are listed in Author response table 1 (in pA/pF):

Author response table 1.

Regarding the assessment of transfection efficacy, we estimated it approximately by using fluorescence proteins as reporters, which were co-expressed with the relevant proteins via the selfcleaving 2A peptide.

7) Greater detail needs to be provided for the generation of NaV1.5 and NaV1.6 chimeras. Specifically, what AA residues were changed between sodium channel isoforms?

We thank reviewer for pointing this out. In the revised manuscript, we have included the specific amino acid residues that were changed between NaV1.5 and NaV1.6 to generate the chimeric constructs.

8) In line 481, the authors refer to Fig. S2d instead of Fig. S6D. This should be corrected. Furthermore, the unusual shift in sodium current kinetics that the authors observe might be due in part to junction potential. Did the authors take that into consideration?

We apologize for this error. The reference to "Fig. S2d" has been corrected to "Fig. S6D" in the revised manuscript.

Regarding the unusual shift observed in the sodium current kinetics, we agree with the reviewer's suggestion that the junction potential may contribute to this phenomenon. During patch-clamp recordings, we ensure that the junction potential was properly compensated by the amplifier. Additionally, the replacement of CsF in pipette solution may have contributed to the observed unusual shift, as CsF in pipette solution has been reported to shift the voltage dependence of activation and fast/slow inactivation of NaV channels towards more negative potentials7.

1. Korngreen A. Advanced patch-clamp analysis for neuroscientists. Neuromethods. Humana Press; 2016:xii, 350 pages.

9) Legends for Fig.S6E and S6F are flipped. Please correct.

We apologize for this error. We have rectified the flipped captions for figure S6E and S6F in the revised manuscript.

10) Variance should be provided for the IC50 values and kinetic parameters of the sodium channels in the supplemental tables.

We thank the reviewer for raising this point. We have included the 95% confidence interval (95%CI) for the IC50 values and kinetic parameters in the revised supplementary tables.

Additionally, we have corrected some equations in the methods section:

1. Line 500 and line 503: We have corrected equation (1) by adding the parameter hill coefficient.

2. Line 514: We have revised equation (4) from to

Author Response

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

We are very grateful to the reviewers for their thoughtful comments on the manuscript and to the editors for their assessment.

We thank the reviewers for their positive feedback and appreciate that they consider our method a valid addition to previously established systems for generating recombinant RNA viruses.

To strengthen this point, we have now included additional validation by the rescue of recombinant Chikungunya and Dengue virus from viral RNA directly, using the CLEVER protocol. This strengthens the potential of this method as a reverse genetics platform for positive-stranded viruses in general.

The supportive data has been amended in the Results section, taken into account in Materials and Methods, and the corresponding supplementary figure (Figure S4) has been added.

One key point raised by one of the reviewers, a comparison with different systems, could not be addressed in this manuscript as our lab does not at all perform BAC cloning. We currently do not have the necessary expertise to conduct an unbiased side-by-side comparison.

All other comments were addressed in detail, either by including additional data or through specific clarification in the revised text. We are grateful for the careful review and constructive criticisms raised by the reviewers and feel that the corrections and additions have significantly improved the manuscript.

We have revised the latest version posted May 30, 2023 on bioRxiv (https://doi.org/10.1101/2023.05.11.540343).

Reviewer #1:

Public Review:

In this manuscript, Kipfer et al describe a method for a fast and accurate SARS-CoV2 rescue and mutagenesis. This work is based on a published method termed ISA (infectious subgenomic amplicons), in which partially overlapping DNA fragments covering the entire viral genome and additional 5' and 3' sequences are transfected into mammalian cell lines. These DNA fragments recombine in the cells, express the full length viral genomic RNA and launch replication and rescue of infectious virus.

CLEVER, the method described here significantly improves on the ISA method to generate infectious SARS-CoV2, making it widely useful to the virology community.

Specifically, the strengths of this method are:

1) The successful use of various cell lines and transfection methods.

2) Generation of a four-fragment system, which significantly improves the method efficiency due to lower number of required recombination events.

3) Flexibility in choice of overlapping sequences, making this system more versatile.

4) The authors demonstrated how this system can be used to introduce point mutations as well as insertion of a tag and deletion of a viral gene.

5) Fast-tracking generation of infectious virus directly from RNA of clinical isolates by RT-PCR, without the need for cloning the fragments or using synthetic sequences.

One weakness of the latter point, which is also pointed out by the authors, is that the direct rescue of clinical isolates was not tested for sequence fidelity.

The manuscript clearly presents the findings, and the proof-of-concept experiments are well designed.

Overall, this is a very useful method for SARS-CoV2 research. Importantly, it can be applicable to many other viruses, speeding up the response to newly emerging viruses than threaten the public health.

We thank the reviewer for this positive feedback and the summary of the main points. Nevertheless, we would like to comment on point 5): “the direct rescue of clinical isolates was not tested for sequence fidelity”

This impression by the reviewer suggests that the data was not sufficient on this point. However, the sequence fidelity after direct rescue from RNA was indeed tested in this study, even on a clonal level (please see: Table S2, or raw NGS data SRX20303605 - SRX20303607). For higher clarity, we added the following sentence to the manuscript:<br /> “Indeed, a slight increase of unintentional mutations was observed when sequencing clonal virus populations rescued from RNA directly”.

Recommendations for the authors:

Minor Points:

1) On page 8, the authors write: "levels correlated very well with the viral phenotype". This sentence is not clear. Please clarify what you mean by "viral phenotype". Do you mean CPE on Vero cells?

We corrected the sentence to: “(…) staining intensity and patterns correlated very well with the wild-type phenotype.”

2) Page 9 "sequences were analyzed with a cut-off of 10%. Cutoff of what? please clarify.

The sentence was rephrased to: “(…)mutations with a relative abundance of >10% in the entire virus population were analyzed”

3) Page 15: The authors refer to the time required for completion of each step of the process. It would be helpful and informative for the readers to include a panel in figure 4, visualizing the timelines.

We included a timeline in Figure 4, Panel A.

4) Materials and methods, first paragraph: Please specify which human samples were collected. Do the authors refer to clinical virus isolates?

We added the following information to the Materials and Methods section:<br /> “Human serum samples for neutralization assays were collected from SARS-CoV-2 vaccinated anonymous donors (…)”

Clinical virus isolates (Material and Methods; Virus) were used for control experiments, neutralization assays, or as templates for RT-PCR.

5) Supplementary figure 4A: The color scheme makes it hard to differentiate between the BA.1 and BA.5 fragments. Please choose colors that are not as similar to each other.

Colors were adapted for better distinction.

Reviewer #2:

Public Review:

The authors of the manuscript have developed and used cloning-free method. It is not entirely novel (rather it is based on previously described ISA method) but it is clearly efficient and useful complementation to the already existing methods. One of strong points of the approach use by authors is that it is very versatile, i.e. can be used in combination with already existing methods and tools. I find it important as many laboratories have already established their favorite methods to manipulate SARS-CoV-2 genome and are probably unwilling to change their approach entirely. Though authors highlight the benefits of their method these are probably not absolute - other methods may be as efficient or as fast. Still, I find myself thinking that for certain purposes I would like to complement my current approach with elements from authors CLEVER method.

The work does not contain much novel biological data - which is expected for a paper dedicated to development of new method (or for improving the existing one). It may be kind of shortcoming as it is commonly expected that authors who have developed new methods apply it for discovery of something novel. The work stops on step of rescue the viruses and confirming their biological properties. This part is done very well and represents a strength of the study. The properties of rescued viruses were also studied using NSG methods that revealed high accuracy of the used method, which is very important as the method relies on use of PCR that is known to generate random mistakes and therefore not always method of choice.

What I found missing is a real head-to-head comparison of the developed system with an existing alternatives, preferably some PCR-free standard methods such as use of BAC clones. There are a lot of comparisons but they are not direct, just data from different studies has been compared. Authors could also be more opened to discuss limitations of the method. One of these seems to be rather low rescue efficiency - 1 rescue event per 11,000 transfected cells. This is much lower compared to infectious plasmid (about 1 event per 100 cells or so) and infectious RNAs (often 1 event per 10 cells, for smaller genomes most of transfected cells become infected). This makes the CLEVER method poorly suitable for generation of large infectious virus libraries and excludes its usage for studies of mutant viruses that harbor strongly attenuating mutations. Many of such mutations may reduce virus genome infectivity by 3-4 orders of magnitude; with current efficiencies the use of CLEVER approach may result in false conclusions (mutant viruses will be classified as non-viable while in reality they are just strongly attenuated).

We thank reviewer 2 for the careful review of our work and the valuable feedback. We agree that a direct comparison with other (PCR-free) methods such as BAC cloning, could be useful for demonstrating the unique benefits of the CLEVER method. However, as our laboratory does not use any BAC or YAC cloning methods, we could not ensure an unbiased side-byside comparison using different techniques.

We would like to highlight the avoidance of any yeast/bacterial cloning steps that render the CLEVER protocol significantly faster and easier to handle. A visualization of the key steps that could be skipped using CLEVER in comparison to common reverse genetics methods is given in Figure 6.

Further, we firmly believe that the benefits of the CLEVER method become especially apparent for large viral genomes such as the one of SARS-CoV-2, where assembly, genome amplification and sequence verification of plasmid DNA are highly inefficient and more timeconsuming than for small viruses like DENV, CHIKV or HIV.

We agree with the reviewer that the overall transfection and recombination efficiencies observed with CLEVER seemed rather low. Although data on transfection/rescue efficiency is known for many techniques and viruses, we did not find any published data on the reconstitution of SARS-CoV-2 or viruses with similar genome sizes. Therefore, a useful comparator for our observations in relation to other techniques is currently simply missing. We therefore emphasize that the efficiencies of CLEVER were achieved with one of the largest plus-stranded RNA virus genomes, and our data can’t be directly compared to transfection efficiencies of short infectious RNAs.

On the contrary, it was rather interesting to observe the very high rescue efficiency of infectious virus progeny. During the two years of establishing and validating the CLEVER protocol, we reached success rates for the genome reconstitution after transfection of >95 %. This was even obtained with highly attenuated mutants including rCoV2∆ORF3678 (joint deletion of ORF3a, ORF6, ORF7a, and ORF8) (Liu et al., 2022)(see Author response image 1). We amended this data in response to the reviewers’ comment and as an example of the successful rescue of an attenuated virus from five overlapping genome fragments (fragments A, B, C, D1, and D2∆ORF3678).

The latter data were not added to the main manuscript since in this case the deletions were introduced using a different method: from the plasmid-based DNA fragment D2∆ORF3678 and not directly from PCR-based mutagenesis.

Further, CLEVER was used for related substantial manipulations, including the complete deletion of the Envelope gene (E) which led to the creation of a single-cycle virus that may serve as a live, replication-incompetent vaccine candidate (Lett et al., 2023).

Author response image 1.

rCoV2∆ORF3678. Detection of intracellular SARS-CoV-2 nucleocapsid protein (N, green) and nuclei (Hoechst, blue) in Vero E6TMPRSS2 cells infected with rCoV2∆ORF3678 by immunocytochemistry. Scalebar is 200 µm in overview and 50 µm in ROI images.

Recommendations for the authors:

The work is nicely presented and the method authors has developed is clearly valuable. As indicated in Public review section the work would benefit from direct comparison of CLEVER with that of infectious plasmid (or RNA) based methods; direct comparison of data would be more convincing that indirect one. Authors should also discuss possible limitations of the method - this is helpful for a reader.

We were not able to perform a direct comparison of CLEVER with other methods (see our statement above).

We added the following section to the discussion: “Along with the advantages of the CLEVER protocol, limitations must be considered: Interestingly, virus was never rescued after transfecting Vero E6 cells, as has been observed previously (Mélade et al., 2022). Whether this is due to low transfection efficiency or the cell’s inability to recombine remains to be elucidated. Other cell lines not tested within this study will have to be tested for efficient recombination and virus production first. Further, the high sequence integrity of rescued virus is highly dependent on the fidelity of the DNA polymerase used for amplification. The use of other enzymes might negatively influence the sequence integrity of recombinant virus, as it has been observed for the direct rescue from viral RNA using a commercially available onestep RT-PCR kit. Another limitation when performing direct mutagenesis is the synthesis of long oligos to create an overlapping region. Repetitive sequences, for example, can impair synthesis, and self-annealing and hairpin formation increase with prolonged oligos.”

Some technical corrections of the text would be beneficial. In all past of the text the use of terms applicable only for DNA or RNA is mixed and creates some confusion. For example, authors state that "the human cytomegalovirus promoter (CMV) was cloned upstream of 5' UTR and poly(A) tail, the hepatitis delta ribozyme (HDVr) and the simian virus 40 polyadenylation signal downstream of the 3' UTR". Strictly speaking it is impossible as such a construct would contain dsDNA sequence (CMV promoter) followed by ssRNA (5'UTR, polyA tail and HDV ribozyme) and then again dsDNA (SV40 terminator). So, better to be correct and add "sequences corresponding to", "dsDNA copies of" to the description of RNA elements

We thank the reviewer for the advice but would like to state that in scientific language it is common to assume that nucleic acid cloning is based on DNA.

We have corrected the description in the Methods section: “The human cytomegalovirus promoter (CMV) was cloned upstream of the DNA sequence of the viral 5’UTR; herein, the first five nucleotides (ATATT) correspond to the 5’UTR of SARS-CoV. Sequences corresponding to the poly(A) tail (n=35), the hepatitis delta virus ribozyme (HDVr), and the simian virus 40 polyadenylation signal (SV40pA) were cloned immediately downstream of the DNA sequence of the viral 3’UTR.”

For ease of reading and for consistent terminology, we kept the original spelling in the rest of the manuscript.

In description of neutralization assay authors have used temperature 34 C for incubation of virus with antibodies as well as for subsequent incubation of infected cells. Why this temperature was used?

The following sentence was added (Materials and Methods; Cells): “A lower incubation temperature was chosen based on previous studies (V’kovski et al., 2021).”

References

Lett MJ, Otte F, Hauser D, Schön J, Kipfer ET, Hoffmann D, Halwe NJ, Ulrich L, Zhang Y, Cmiljanovic V, Wylezich C, Urda L, Lang C, Beer M, Mittelholzer C, Klimkait T. 2023. Single-cycle SARS-CoV-2 vaccine elicits high protection and sterilizing immunity in hamsters. doi:10.1101/2023.05.17.541127

Liu Y, Zhang X, Liu J, Xia H, Zou J, Muruato AE, Periasamy S, Kurhade C, Plante JA, Bopp NE, Kalveram B, Bukreyev A, Ren P, Wang T, Menachery VD, Plante KS, Xie X, Weaver SC, Shi P-Y. 2022. A live-attenuated SARS-CoV-2 vaccine candidate with accessory protein deletions. Nat Commun 13:4337. doi:10.1038/s41467-022-31930-z

V’kovski P, Gultom M, Kelly JN, Steiner S, Russeil J, Mangeat B, Cora E, Pezoldt J, Holwerda M, Kratzel A, Laloli L, Wider M, Portmann J, Tran T, Ebert N, Stalder H, Hartmann R, Gardeux V, Alpern D, Deplancke B, Thiel V, Dijkman R. 2021. Disparate temperaturedependent virus–host dynamics for SARS-CoV-2 and SARS-CoV in the human respiratory epithelium. PLoS Biol 19:e3001158. doi:10.1371/journal.pbio.3001158

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study addresses how faces and bodies are integrated in two STS face areas revealed by fMRI in the primate brain. It builds upon recordings and analysis of the responses of large populations of neurons to three sets of images, that vary face and body positions. These sets allowed the authors to thoroughly investigate invariance to position on the screen (MC HC), to pose (P1 P2), to rotation (0 45 90 135 180 225 270 315), to inversion, to possible and impossible postures (all vs straight), to the presentation of head and body together or in isolation. By analyzing neuronal responses, they found that different neurons showed preferences for body orientation, head orientation, or the interaction between the two. By using a linear support vector machine classifier, they show that the neuronal population can decode head-body angle presented across orientations, in the anterior aSTS patch (but not middle mSTS patch), except for mirror orientation.

Strengths:

These results extend prior work on the role of Anterior STS fundus face area in face-body integration and its invariance to mirror symmetry, with a rigorous set of stimuli revealing the workings of these neuronal populations in processing individuals as a whole, in an important series of carefully designed conditions.

Minor issues and questions that could be addressed by the authors:

(1) Methods. While monkeys certainly infer/recognize that individual pictures refer to the same pose with varying orientations based on prior studies (Wang et al.), I am wondering whether in this study monkeys saw a full rotation of each of the monkey poses as a video before seeing the individual pictures of the different orientations, during recordings.

The monkeys had not been exposed to videos of a rotating monkey pose before the recordings. However, they were reared and housed with other monkeys, providing them with ample experience of monkey poses from different viewpoints.

(2) Experiment 1. The authors mention that neurons are preselected as face-selective, body-selective, or both-selective. Do the Monkey Sum Index and ANOVA main effects change per Neuron type?

We have performed a new analysis to assess whether the Monkey Sum Index is related to the response strength for the face versus the body as measured in the Selectivity Test of Experiment 1. To do this we selected face- and body-category selective neurons, as well as neurons responding selectively to both faces and bodies. First, we selected those neurons that responded significantly to either faces, bodies, or the two control object categories, using a split-plot ANOVA for these 40 stimuli. From those neurons, we selected face-selective ones having at least a twofold larger mean net response to faces compared to bodies (faces > 2 * bodies) and the control objects for faces (faces  > 2* objects). Similarly, a body-selective neuron was defined by a twofold larger mean net response to bodies compared to faces and the control objects for bodies. A body-and-face selective neuron was defined as having a twofold larger net response to the faces compared to their control objects, and to bodies compared to their control objects, with the ratio between mean response to bodies and faces being less than twofold. Then, we compared the distribution of the Monkey Sum Index (MSI) for each region (aSTS; mSTS), pose (P1, P2), and centering (head- (HC) or monkey-centered (MC)) condition. Too few body-and-face selective neurons were present in each combination of region, pose, and centering (a maximum of 7) to allow a comparison of their MSI distribution with the other neuron types. The Figure below shows the distribution of the MSI for the different orientation-neuron combinations for the body- and face-selective neurons (same format as in Figure 3a, main text). The number of body-selective neurons, according to the employed criteria, varied from 21 to 29, whereas the number of face-selective neurons ranged from 14 to 24 (pooled across monkeys). The data of the two subjects are shown in a different color and the number of cases for each subject is indicated (n1: number of cases for M1; n2: number of cases for M2). The arrows indicate the medians for the data pooled across the monkey subjects. For the MC condition, the MSI tended to be more negative (i.e. relatively less response to the monkey compared to the sum of the body and face responses) for the face compared to the body cells, but this was significant only for mSTS and P1 (p = 0.043; Wilcoxon rank sum test; tested after averaging the indices per neuron to avoid dependence of indices within a neuron). No consistent, nor significant tendencies were observed for the HC stimuli. This absence of a consistent relationship between MSI and face- versus body-selectivity is in line with the absence of a correlation between the MSI and face- versus body-selectivity using natural images of monkeys in a previous study (Zafirova Y, Bognár A, Vogels R. Configuration-sensitive face-body interactions in primate visual cortex. Prog Neurobiol. 2024 Jan;232:102545).

We did not perform a similar analysis for the main effects of the two-way ANOVA because the very large majority of neurons showed a significant effect of body orientation and thus no meaningful difference between the two neuron types can be expected.

Author response image 1.

(3) I might have missed this information, but the correlation between P1 and P2 seems to not be tested although they carry similar behavioral relevance in terms of where attention is allocated and where the body is facing for each given head-body orientation.

Indeed, we did not compute this correlation between the responses to the sitting (P1) and standing (P2) pose avatar images. However, as pointed out by the reviewer, one might expect such correlations because of the same head orientations and body-facing directions. Thus, we computed the correlation between the 64 head-body orientation conditions of P1 and P2 for those neurons that were tested with both poses and showed a response for both poses (Split-plot ANOVA). This was performed for the Head-Centered and Monkey-Centered tests of Experiment 1 for each monkey and region. Note that not all neurons were tested with both poses (because of failure to maintain isolation of the single unit in both tests or the monkey stopped working) and not all neurons that were recorded in both tests showed a significant response for both poses, which is not unexpected since these neurons can be pose selective. The distribution of the Pearson correlation coefficients of the neurons with a significant response in both tests is shown in Figure S1. The median correlation coefficient was significantly larger than zero for each region, monkey, and centering condition (outcome of Wilcoxon tests, testing whether the median was different from zero (p1 = p-value for M1; p2: p-value for M2) in Figure), indicating that the effect of head and/or body orientation generalizes across pose. We have noted this now in the Results (page 12) and added the Figure (New Figure S1) in the Suppl. Material.

(4) Is the invariance for position HC-MC larger in aSTS neurons compared to mSTS neurons, as could be expected from their larger receptive fields?

Yes, the position tolerance of the interaction of body and head orientation was significantly larger for aSTS compared to mSTS neurons, as we described on pages 11 and 12 of the Results. This is in line with larger receptive fields in aSTS than in mSTS. However, we did not plot receptive fields in the present study.

(5) L492 "The body-inversion effect likely results from greater exposure to upright than inverted bodies during development". Monkeys display more hanging upside-down behavior than humans, however, does the head appear more tilted in these natural configurations?

Indeed, infant monkeys do spend some time hanging upside down from their mother's belly. While we lack quantitative data on this behavior, casual observations suggest that even young monkeys spend more time upright. The tilt of the head while hanging upside down can vary, just as it does in standing or sitting monkeys (as when they search for food or orient to other individuals). To our knowledge, no quantitative data exist on the frequency of head tilts in upright versus upside-down monkeys. Therefore, we refrain from further speculation on this interesting point, which warrants more attention.

(6) Methods in Experiment 1. SVM. How many neurons are sufficient to decode the orientation?

The number of neurons that are needed to decode the head-body orientation angle depends on which neurons are included, as we show in a novel analysis of the data of Experiment 1. We employed a neuron-dropping analysis, similar to Chiang et al. (Chiang FK, Wallis JD, Rich EL. Cognitive strategies shift information from single neurons to populations in prefrontal cortex. Neuron. 2022 Feb 16;110(4):709-721) to assess the positive (or negative) contribution of each neuron to the decoding performance. We performed cross-validated linear SVM decoding N times, each time leaving out a different neuron (using N-1 neurons; 2000 resamplings of pseudo-population vectors). We then ranked decoding accuracies from highest to lowest, identifying the ‘worst’ (rank 1) to ‘best’ (rank N) neurons. Next, we conducted N decodings, incrementally increasing the number of included neurons from 1 to N, starting with the worst-ranked neuron (rank 1) and sequentially adding the next (rank 2, rank 3, etc.). This analysis focused on zero versus straight angle decoding in the aSTS, as it yielded the highest accuracy. We applied it when training on MC and testing on HC for each pose. Plotting accuracy as a function of the number of included neurons suggested that less than half contributed positively to decoding. We show also the ten “best” neurons for each centering condition and pose. These have a variety of tuning patterns for head and body orientation suggesting that the decoding of head-body orientation angle depends on a population code. Notably, the best-ranked (rank N) neuron alone achieved above-chance accuracy. We have added this interesting and novel result to the Results (page 16) and Suppl. Material (new Figure S3).

(7) Figure 3D 3E. Could the authors please indicate for each of these neurons whether they show a main effect of face, body, or interaction, as well as their median corrected correlation to get a flavor of these numbers for these examples?

We have indicated these now in Figure 3.

(8) Methods and Figure 1A. It could be informative to precise whether the recordings are carried in the lateral part of the STS or in the fundus of the STS both for aSTS and mSTS for comparison to other studies that are using these distinctions (AF, AL, MF, ML).

In experiment 1, the recording locations were not as medial as the fundus. For experiments 2 and 3, the ventral part of the fundus was included, as described in the Methods. We have added this to the Methods now (page 31).

Wang, G., Obama, S., Yamashita, W. et al. Prior experience of rotation is not required for recognizing objects seen from different angles. Nat Neurosci 8, 1768-1775 (2005). https://doi-org.insb.bib.cnrs.fr/10.1038/nn1600

Reviewer #2 (Public review):

Summary:

This paper investigates the neuronal encoding of the relationship between head and body orientations in the brain. Specifically, the authors focus on the angular relationship between the head and body by employing virtual avatars. Neuronal responses were recorded electrophysiologically from two fMRI-defined areas in the superior temporal sulcus and analyzed using decoding methods. They found that: (1) anterior STS neurons encode head-body angle configurations; (2) these neurons distinguish aligned and opposite head-body configurations effectively, whereas mirror-symmetric configurations are more difficult to differentiate; and (3) an upside-down inversion diminishes the encoding of head-body angles. These findings advance our understanding of how visual perception of individuals is mediated, providing a fundamental clue as to how the primate brain processes the relationship between head and body - a process that is crucial for social communication.

Strengths:

The paper is clearly written, and the experimental design is thoughtfully constructed and detailed. The use of electrophysiological recordings from fMRI-defined areas elucidated the mechanism of head-body angle encoding at the level of local neuronal populations. Multiple experiments, control conditions, and detailed analyses thoroughly examined various factors that could affect the decoding results. The decoding methods effectively and consistently revealed the encoding of head-body angles in the anterior STS neurons. Consequently, this study offers valuable insights into the neuronal mechanisms underlying our capacity to integrate head and body cues for social cognition-a topic that is likely to captivate readers in this field.

Weaknesses:

I did not identify any major weaknesses in this paper; I only have a few minor comments and suggestions to enhance clarity and further strengthen the manuscript, as detailed in the Private Recommendations section.

Reviewer #3 (Public review):

Summary:

Zafirova et al. investigated the interaction of head and body orientation in the macaque superior temporal sulcus (STS). Combining fMRI and electrophysiology, they recorded responses of visual neurons to a monkey avatar with varying head and body orientations. They found that STS neurons integrate head and body information in a nonlinear way, showing selectivity for specific combinations of head-body orientations. Head-body configuration angles can be reliably decoded, particularly for neurons in the anterior STS. Furthermore, body inversion resulted in reduced decoding of head-body configuration angles. Compared to previous work that examined face or body alone, this study demonstrates how head and body information are integrated to compute a socially meaningful signal.

Strengths:

This work presents an elegant design of visual stimuli, with a monkey avatar of varying head and body orientations, making the analysis and interpretation straightforward. Together with several control experiments, the authors systematically investigated different aspects of head-body integration in the macaque STS. The results and analyses of the paper are mostly convincing.

Weaknesses:

(1) Using ANOVA, the authors demonstrate the existence of nonlinear interactions between head and body orientations. While this is a conventional way of identifying nonlinear interactions, it does not specify the exact type of the interaction. Although the computation of the head-body configuration angle requires some nonlinearity, it's unclear whether these interactions actually contribute. Figure 3 shows some example neurons, but a more detailed analysis is needed to reveal the diversity of the interactions. One suggestion would be to examine the relationship between the presence of an interaction and the neural encoding of the configuration angle.

This is an excellent suggestion. To do this, one needs to identify the neurons that contribute to the decoding of head-body orientation angles. For that, we employed a neuron-dropping analysis, similar to Chiang et al. (Chiang FK, Wallis JD, Rich EL. Cognitive strategies shift information from single neurons to populations in prefrontal cortex. Neuron. 2022 Feb 16;110(4):709-721.) to assess the positive (or negative) contribution of each neuron to the decoding performance. We performed cross-validated linear SVM decoding N times, each time leaving out a different neuron (using N-1 neurons; 2000 resamplings of pseudo-population vectors). We then ranked decoding accuracies from highest to lowest, identifying the ‘worst’ (rank 1) to ‘best’ (rank N) neurons. Next, we conducted N decodings, incrementally increasing the number of included neurons from 1 to N, starting with the worst-ranked neuron (rank 1) and sequentially adding the next (rank 2, rank 3, etc.). This analysis focused on zero versus straight angle decoding in the aSTS, as it yielded the highest accuracy. We applied it when training on MC and testing on HC for each pose. Plotting accuracy as a function of the number of included neurons suggested that less than half contributed positively to decoding (see Figure S3). We examined the tuning for head and body orientation of the 10 “best” neurons (Figure S3). For half or more of those the two-way ANOVA showed a significant interaction. These are indicated by the red color in the Figure. They showed a variety of tuning patterns for head and body orientation, suggesting that the decoding of the head-body orientation angle results from a combination of neurons with different tuning profiles. Based on a suggestion from reviewer 2, we performed for each neuron of experiment 1 a one-way ANOVA with as factor head-body orientation angle. To do that, we combined all 64 trials that had the same head-body orientation angle. The percentage of neurons (required to be responsive in the tested condition) for which this one-way ANOVA was significant was low but larger than the expected 5% (Type 1 error), with a median of 16.5% (range: 3 to 23%) in aSTS and 8% for mSTS (range: 0-19%). However, a higher percentage of the 10 best neurons for each pose (indicated by the star) showed a significant one-way ANOVA for angle (for P1, MC: 50% (95% confidence interval (CI): 19% – 81%); P1, HC: 70% (CI: 35% - 93%); P2, MC: 70% (CI: 35% – 93%); P2: HC: 50% (CI: 19%-81%)). These percentages were significantly higher than expected for a random sample from the population of neurons for each pose-centering combination (expected percentages listed in the same order as above: 16%, 13%, 16%, and 10%; all outside CI). Thus, for at least half of the “best” neurons, the response differed significantly among the head-orientation angles at the single neuron level. Nonetheless, the tuning profiles were diverse, suggesting a populationl code for head-body orientation angle. We have added this interesting and novel result to the Results (page 16) and Suppl. Material (Figure S3).

(2) Figure 4 of the paper shows a better decoding of the configuration angle in the anterior STS than in the middle STS. This is an interesting result, suggesting a transformation in the neural representation between these two areas. However, some control analyses are needed to further elucidate the nature of this transformation. For example, what about the decoding of head and body orientations - dose absolute orientation information decrease along the hierarchy, accompanying the increase in configuration information?

We have performed now two additional analyses, one in which we decoded the orientation of the head and another one in which we decoded the orientation of the body. We employed the responses to the avatar of experiment 1, using the same sample of neurons of which we decoded the head-body orientation angle. To decode the head orientation, the trials with identical head orientation, irrespective of their body orientation, were given the same label. For this, we employed only responses in the head-centered condition. To decode the body orientation, the trials with identical body orientation, irrespective of their head orientation, had the same label, and we employed only responses in the body-centered condition. The decoding was performed separately for each pose (P1 and P2) and region. We decoded either the responses of 20 neurons (10 randomly sampled from each monkey for each of the 1000 resamplings), 40 neurons (20 randomly sampled per monkey), or 60 neurons (30 neurons per monkey) since the sample of 60 neurons yielded close to ceiling performance for the body orientation decoding. For each pose, the body orientation decoding was worse for aSTS than for mSTS, although this difference reached significance only for P1 and for the 40 neurons sample of P2 (p < 0.025; two-tailed test; same procedure as employed for testing the significance of the decoding of whole-body orientation for upright versus inverted avatars (Experiment 3))). Face orientation decoding was significantly worse for aSTS compared to mSTS. These results are in line with the previously reported decreased decoding of face orientation in the anterior compared to mid-STS face patches (Meyers EM, Borzello M, Freiwald WA, Tsao D. Intelligent information loss: the coding of facial identity, head pose, and non-face information in the macaque face patch system. J Neurosci. 2015 May 6;35(18):7069-81), and decreased decoding of body orientation in anterior compared to mid-STS body patches (Kumar S, Popivanov ID, Vogels R. Transformation of Visual Representations Across Ventral Stream Body-selective Patches. Cereb Cortex. 2019 Jan 1;29(1):215-229). As mentioned by the reviewer, this contrasts with the decoding of the head-body orientation angle, which increases when moving more anteriorly. We mention this finding now in the Discussion (page 27) and present the new Figure S10 in the Suppl. Material.    

(3) While this work has characterized the neural integration of head and body information in detail, it's unclear how the neural representation relates to the animal's perception. Behavioural experiments using the same set of stimuli could help address this question, but I agree that these additional experiments may be beyond the scope of the current paper. I think the authors should at least discuss the potential outcomes of such experiments, which can be tested in future studies.

Unfortunately, we do not have behavioral data. One prediction would be that the discrimination of head-body orientation angle, irrespective of the viewpoint of the avatar, would be more accurate for zero versus straight angles compared to the right versus left angles. We have added this to the Discussion (page 28).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) P22 L373. It should read Figure S5C instead of S4C.

Thanks; corrected.

(2) Figure 7B. All inverted decoding accuracies, although significantly lower than upright decoding accuracies, appear significantly above baseline. Should the title be amended accordingly?

Thanks for pointing this out. To avoid future misunderstanding we have changed the title to:

“Integration of head and body orientations in the macaque superior temporal sulcus is stronger for upright bodies”

(3) Discussion L432-33. "with some neurons being tuned to a particular orientation of both the head and the body". Wouldn't that be visible as a diagonal profile on the normalized net responses in Fig 3D? Or can the Anova evidence such a tuning?

We meant to say that some neurons were tuned to a particular combination of head and body orientation, like the third aSTS example neuron shown in Figure 3D. We have corrected the sentence.

Reviewer #2 (Recommendations for the authors):

Major comment:

This paper effectively demonstrates that the angular relationship between the head and body can be decoded from population responses in the anterior STS. In other words, these neurons encode information about the head-body angle. However, how exactly do these neurons encode this information? Given that the study employed electrophysiological recordings from a local population of neurons, it might be possible to provide additional data on the response patterns of individual neurons to shed light on the underlying encoding mechanisms.

Although the paper already presents example response patterns (Figures 3D, E) and shows that STS neurons encode interactions between head and body orientations (Figure 3B), it remains unclear whether the angle difference between the head and body has a systematic effect on neuronal responses. For instance, a description of whether some neurons preferentially encode specific head-body angle differences (e.g., a "45-degree angle neuron"), or additional population analyses such as a one-way ANOVA with angle difference as the main effect (or two-way ANOVA with angle difference as one of the main effect), would be very informative. Such data could offer valuable insights into how individual neurons contribute to the encoding of head-body angle differences-a detail that may also be reflected in the decoding results. Alternatively, it is possible that the encoding of head-body angle is inherently complex and only discernible via decoding methods applied to population activity. Either scenario would provide interesting and useful information to the field.

We have performed two additional analyses which are relevant to this comment. First, we attempted to relate the tuning for body and head orientation with the decoding of the head-body orientation angle. To do this, one needs to identify the neurons that contribute to the decoding of head-body orientation angles. For that, we employed a neuron-dropping analysis, similar to Chiang et al. (Chiang FK, Wallis JD, Rich EL. Cognitive strategies shift information from single neurons to populations in prefrontal cortex. Neuron. 2022 Feb 16;110(4):709-721.) to assess the positive (or negative) contribution of each neuron to the decoding performance. We performed cross-validated linear SVM decoding N times, each time leaving out a different neuron (using N-1 neurons; 2000 resamplings of pseudo-population vectors). We then ranked decoding accuracies from highest to lowest, identifying the ‘worst’ (rank 1) to ‘best’ (rank N) neurons. Next, we conducted N decodings, incrementally increasing the number of included neurons from 1 to N, starting with the worst-ranked neuron (rank 1) and sequentially adding the next (rank 2, rank 3, etc.). This analysis focused on zero versus straight angle decoding in the aSTS, as it yielded the highest accuracy. We applied it when training on MC and testing on HC for each pose. Plotting accuracy as a function of the number of included neurons suggested that less than half contributed positively to decoding (see Figure S3). We examined the tuning for head and body orientation of the 10 “best” neurons (Figure S3). For half or more of those the two-way ANOVA showed a significant interaction. These are indicated by the red color in the Figure. They showed a variety of tuning patterns for head and body orientation, suggesting that the decoding of the head-body orientation angle results from a combination of neurons with different tuning profiles.

Second, we have followed the suggestion of the reviewer to perform for each neuron of experiment 1 a one-way ANOVA with as factor head-body orientation angle. To do that, we combined all 64 trials that had the same head-body orientation angle. The percentage of neurons (required to be responsive in the tested condition) for which this one-way ANOVA was significant is shown in the Tables below for each region, separately for each pose (P1, P2), centering condition (MC = monkey-centered; HC = head-centered) and monkey subject (M1, M2). The percentages were low but larger than the expected 5% (Type 1 error), with a median of 16.5% (range: 3 to 23%) in aSTS and 8% for mSTS (range: 0-19%).

Author response table 1.

Interestingly, a higher percentage of the 10 best neurons for each pose (indicated by the star in the Figure above) showed a significant one-way ANOVA for angle (for P1, MC: 50% (95% confidence interval (CI): 19% – 81%); P1, HC: 70% (CI: 35% - 93%); P2, MC: 70% (CI: 35% – 93%); P2: HC: 50% (CI: 19%-81%)). These percentages were significantly higher than expected for a random sample from the population of neurons for each pose-centering combination (expected percentages listed in the same order as above: 16%, 13%, 16%, and 10%; all outside CI). Thus, for at least half of the “best” neurons, the response differed significantly among the head-orientation angles at the single neuron level. Nonetheless, the tuning profiles were quite diverse, suggesting population coding of head-body orientation angle. We have added this interesting and novel result to the Results (page 16) and Suppl. Material (Figure S3).    

Minor comments:

(1) Figure 4A, Fourth Row Example (Zero Angle vs. Straight Angle, Bottom of the P2 Examples): The order of the example stimuli might be incorrect- the 0{degree sign} head with 180{degree sign} body stimulus (leftmost) might be swapped with the 180{degree sign} head with 0{degree sign} body stimulus (5th from the left). While this ordering may be acceptable, please double-check whether it reflects the authors' intended arrangement.

We have changed the order of the two stimuli in Figure 4A, following the suggestion of the reviewer.

(2) Page 12, Lines 192-194: The text states, "Interestingly, some neurons (e.g. Figure 3D) were tuned to a particular combination of a head and body irrespective of centering." However, Figure 3D displays data for a total of 10 neurons. Could you please specify which of these neurons are being referred to in this context?

The wording was not optimal. We meant to say that some neurons were tuned to a particular combination of head and body orientation, like the third aSTS example neuron of Figure 3D. We have rephrased the sentence and clarified which example neuron we referred to.

(3) Page 28, Lines 470-471: The text states, "We observed no difference in response strength between anatomically possible and impossible configurations." Please clarify which data were compared for response strength, as I could not locate the corresponding analyses.

The anatomically possible and impossible configurations differ in the head-body orientation angle. However, as we reported before in the Results, there was no effect of head-body orientation angle on mean response strength across poses (Friedman ANOVA; all p-values for both poses and centerings > 0.1). We have clarified this now in the Discussion (page 28).

(4) Pages 40-43, Decoding Analyses: In experiments 2 and 3, were the decoding analyses performed on simultaneously recorded neurons? If so, such analyses might leverage trial-by-trial correlations and thus avoid confounds from trial-to-trial variability. In contrast, experiment 1, which used single-shank electrodes, would lack this temporal information. Please clarify how trial numbers were assigned to neurons in each experiment and how this assignment may have influenced the decoding performance.

For the decoding analyses of experiments 2 and 3, we combined data from different daily penetrations, with only units from the same penetration being recorded simultaneously. In the decoding analyses of each experiment, the trials were assigned randomly to the pseudo-population vectors, shuffling on each resampling the trial order per neuron. This shuffling abolishes noise correlations in the analysis of each experiment.

(5) Page 41, Lines 792-802: The authors state that "To assess the significance of the differences in classification scores between pairs of angles ... we computed the difference in classification score between the two pairs for each resampling and the percentile of 0 difference corresponded to the p-value." In a two-sided test under the null hypothesis of no difference between the distributions, the conventional approach would be to compute the p-value as the proportion of resampled differences that are as extreme or more extreme than the observed difference. Since a zero difference might be relatively rare, relying solely on its percentile could potentially misrepresent the tail probabilities relevant to a two-sided test. Could you clarify how their method addresses this issue?

This test is based on the computation of the distribution of the difference between classification accuracies across resamplings. This is similar to the computation of the confidence interval of a  difference. Thus, we assess whether the theoretical zero value (= no difference; = null hypothesis) is outside the 2.5 and 97.5 percentile interval of the computed distribution of the empirically observed differences. We clarified now in the Methods (page 41) that for a two-tailed test the computed p-value (the percentile of the zero value) should be smaller than 0.025.

(6) Page 43, Lines 829-834: The manuscript explains: "The mean of 10 classification accuracies (i.e., of 10 resamplings) was employed to obtain a distribution (n=100) of the differences in classification accuracy ... The reported standard deviations of the classification accuracies are computed using also the means of 10 resamplings." I am unfamiliar with this type of analysis and am unclear about the rationale for calculating distributions and standard deviations based on the means of 10 resamplings rather than using the original distribution of classification accuracies. This resampling procedure appears to yield a narrower distribution and smaller standard deviations than the original data. Could you please justify this approach?

The logic of the analysis is to reduce the noise in the data, by averaging across 10 randomly selected resamplings, but still keeping a sufficient number of data (100 values) for a test.

Reviewer #3 (Recommendations for the authors):

(1) Some sentences are too long and difficult to parse. For example, in line 177: "the correlations between the responses to the 64 head-body orientation conditions of the two centerings for the neuron and pose combinations showing significant head-body interactions for the two centerings were similar to those observed for the whole population."

We have modified this sentence: For neuron and pose combinations with significant head-body interactions in both centerings, the correlations between responses to the 64 head-body orientation conditions were similar to those observed in the whole population.

(2) The authors argue in line 485: "in our study, a search bias cannot explain the body-inversion effect since we selected responsive units using both upright and inverted images." However, the body-selective patches were localized using upright images, correct?

The monkey-selective patches were localized using upright images indeed. However, we recorded in experiment 3 (and 2) also outside the localized patches (as we noted before in the Methods:  “In experiments 2 and 3 we recorded from a wider region, which overlapped with the two monkey patches and the recording locations of experiment 1”). Furthermore, the preference for upright monkey images is not an all-or-nothing phenomenon: most units still responded to inverted monkeys. Also, we believe it is likely that the mean responses to the inverted bodies in the monkey patches, defined by upright bodies versus objects, would be larger than those to objects and we would be surprised to learn that there is a patch selective for inverted bodies that we would have missed with our localizer.

(3) Typo: line 447, "this independent"->"is independent"?

Corrected.

Author response:

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

Reviewer #1 (Public Review): 

Summary: 

Campbell et al investigated the effects of light on the human brain, in particular the subcortical part of the hypothalamus during auditory cognitive tasks. The mechanisms and neuronal circuits underlying light effects in non-image forming responses are so far mostly studied in rodents but are not easily translated in humans. Therefore, this is a fundamental study aiming to establish the impact light illuminance has on the subcortical structures using the high-resolution 7T fMRI. The authors found that parts of the hypothalamus are differently responding to illuminance. In particular, they found that the activity of the posterior hypothalamus increases while the activity of the anterior and ventral parts of the hypothalamus decreases under high illuminance. The authors also report that the performance of the 2-back executive task was significantly better in higher illuminance conditions. However, it seems that the activity of the posterior hypothalamus subpart is negatively related to the performance of the executive task, implying that it is unlikely that this part of the hypothalamus is directly involved in the positive impact of light on performance observed. Interestingly, the activity of the posterior hypothalamus was, however, associated with an increased behavioural response to emotional stimuli. This suggests that the role of this posterior part of the hypothalamus is not as simple regarding light effects on cognitive and emotional responses. This study is a fundamental step towards our better understanding of the mechanisms underlying light effects on cognition and consequently optimising lighting standards. 

Strengths: 

While it is still impossible to distinguish individual hypothalamic nuclei, even with the highresolution fMRI, the authors split the hypothalamus into five areas encompassing five groups of hypothalamic nuclei. This allowed them to reveal that different parts of the hypothalamus respond differently to an increase in illuminance. They found that higher illuminance increased the activity of the posterior part of the hypothalamus encompassing the MB and parts of the LH and TMN, while decreasing the activity of the anterior parts encompassing the SCN and another part of TMN. These findings are somewhat in line with studies in animals. It was shown that parts of the hypothalamus such as SCN, LH, and PVN receive direct retinal input in particular from ipRGCs. Also, acute chemogenetic activation of ipRGCs was shown to induce activation of LH and also increased arousal in mice. 

Weaknesses: 

While the light characteristics are well documented and EDI calculated for all of the photoreceptors, it is not very clear why these irradiances and spectra were chosen. It would be helpful if the authors explained the logic behind the four chosen light conditions tested. Also, the lights chosen have cone-opic EDI values in a high correlation with the melanopic EDI, therefore we can't distinguish if the effects seen here are driven by melanopsin and/or other photoreceptors. In order to provide a more mechanistic insight into the light-driven effects on cognition ideally one would use a silent substitution approach to distinguish between different photoreceptors. This may be something to consider when designing the follow-up studies. 

Reviewer #1 (Recommendations For The Authors): 

(1) As suggested in the public review more information regarding the reasons behind the chosen light condition is needed. 

While the light characteristics are well documented and EDI calculated for all of the photoreceptors, it is not very clear why these irradiances and spectra were chosen. It would be helpful if the authors explained the logic behind the four chosen light conditions tested. Also, the lights chosen have cone-opic EDI values in a high correlation with the melanopic EDI, therefore we can't distinguish if the effects seen here are driven by melanopsin or cone opsins. In order to provide a more mechanistic insight into the light-driven effects on cognition ideally one would use a silent substitution approach to distinguish between different photoreceptors. 

(2) In support of this work, it was shown in mice that acute activation of ipRGCs using chemogenetics induces c-fos in some of the hypothalamic brain areas discussed here including LH (Milosavljevic et al, 2016 Curr Biol). Another study to consider including in the discussion is by Sonoda et al 2020 Science, in which the authors showed that a subset of ipRGCs release GABA. 

(3) Figure 1 looks squashed, especially the axes. Also, Figure 2 looks somewhat blurry. I would suggest that the authors edit the figures to correct this.

We thank the reviewer for their positive comments and agree with the weaknesses they pointed out. 

(1) The explanation regarding the choice of the illuminance is now included in the revised manuscript (PAGE 17): “Blue-enriched light illuminances were set according to the technical characteristics of the light source and to keep the overall photon flux similar to prior 3T MRI studies of our team (between ~1012 and 1014 ph/cm²/s) (Vandewalle et al., 2010, 2011). The orange light was introduced as a control visual stimulation for potential secondary whole-brain analyses. For the present region of interest analyses, we discarded colour differences between the light conditions and only considered illuminance as indexed by mel EDI lux. This constitutes a limitation of our study as it does not allow attributing the findings to a particular photoreceptor class.”

The revised discussion makes clear that these choices limit the interpretation about the photoreceptors involved (PAGES 12-13): “We based our rationale and part of our interpretations on ipRGC projections, which have been demonstrated in rodents to channel the NIF biological impact of light and incorporate the inputs from rods and cones with their intrinsic photosensitivity into a light signal that can impact the brain (Güler et al., 2008; Tri & Do, 2019). Given the polychromatic nature of the light we used, classical photoreceptors and their projections to visual brain areas are, however, very likely to have directly or indirectly contributed to the modulation by light of the regional activity of the hypothalamus.”

The discussion also points out the promises of silent substitution (PAGE 13): “Future human studies could isolate the contribution of each photoreceptor class to the impact of light on cognitive brain functions by manipulating prior light history (Chellappa et al., 2014) or through the use of silent substitutions between metameric light exposures (Viénot et al., 2012)”.

(2) We now refer to the studies by Milosavljevic et al. and Sonoda et al. 

PAGE 9: “Our data may therefore be compatible with an increase in orexin release by the LH with increasing illuminance. In line with this assumption, chemoactivation of ipRGCs lead to increase c-fos production, a marker of cellular activation, over several nuclei of the hypothalamus, including the lateral hypothalamus (Milosavljevic et al., 2016). If this initial effect of light we observe over the posterior part of the hypothalamus was maintained over a longer period of exposure, this would stimulate cognition and maintain or increase alertness (Campbell et al., 2023) and may also be part of the mechanisms through which daytime light increases the amplitude in circadian variations of several physiological features (BanoOtalora et al., 2021; Dijk et al., 2012).”

PAGE 10: “Chemoactivation of ipRGCs in rodents led to an increase activity of the SCN, over the inferior anterior hypothalamus, but had no impact on the activity of the VLPO, over the superior anterior hypothalamus (Milosavljevic et al., 2016). How our findings fit with these fine-grained observations and whether there are species-specific differences in the responses to light over the different part of the hypothalamus remains to be established.”

PAGE 10: “In terms of chemical communication, these changes in activity could be the results of an inhibitory signal from a subclass of ipRGCs, potentially through the release aminobutyric acid (GABA), as a rodent study found that a subset of ipRGCs release GABA at brain targets including the SCN (and intergeniculate leaflet and ventral lateral geniculate nucleus), leading to a reduction in the ability of light to affect pupil size and circadian photoentrainment (Sonoda et al., 2020). Whatever the signalling of ipRGC, our finding over the anterior hypothalamus could correspond to a modification of GABA signalling of the SCN which has been reported to have excitatory properties, such that the BOLD signal changes we report may correspond to a reduction in excitation arising in part from the SCN (Albers et al., 2017).”

(3) Figures 1 and 2 were modified. We hope their quality is now satisfactory. We are willing to provide separate figures prior to publication of the Version of Record.

Reviewer #2 (Public Review): 

Summary 

The interplay between environmental factors and cognitive performance has been a focal point of neuroscientific research, with illuminance emerging as a significant variable of interest. The hypothalamus, a brain region integral to regulating circadian rhythms, sleep, and alertness, has been posited to mediate the effects of light exposure on cognitive functions. Previous studies have illuminated the role of the hypothalamus in orchestrating bodily responses to light, implicating specific neural pathways such as the orexin and histamine systems, which are crucial for maintaining wakefulness and processing environmental cues. Despite advancements in our understanding, the specific mechanisms through which varying levels of light exposure influence hypothalamic activity and, in turn, cognitive performance, remain inadequately explored. This gap in knowledge underscores the need for high-resolution investigations that can dissect the nuanced impacts of illuminance on different hypothalamic regions. Utilizing state-of-the-art 7 Tesla functional magnetic resonance imaging (fMRI), the present study aims to elucidate the differential effects of light on the hypothalamic dynamics and establish a link between regional hypothalamic activity and cognitive outcomes in healthy young adults. By shedding light on these complex interactions, this research endeavours to contribute to the foundational knowledge necessary for developing innovative therapeutic strategies aimed at enhancing cognitive function through environmental modulation. 

Strengths: 

(1) Considerable Sample Size and Detailed Analysis: The study leverages a robust sample size and conducts a thorough analysis of hypothalamic dynamics, which enhances the reliability and depth of the findings. 

(2) Use of High-Resolution Imaging: Utilizing 7 Tesla fMRI to analyze brain activity during cognitive tasks offers high-resolution insights into the differential effects of illuminance on hypothalamic activity, showcasing the methodological rigor of the study. 

(3) Novel Insights into Illuminance Effects: The manuscript reveals new understandings of how different regions of the hypothalamus respond to varying illuminance levels, contributing valuable knowledge to the field. 

(4) Exploration of Potential Therapeutic Applications: Discussing the potential therapeutic applications of light modulation based on the findings suggests practical implications and future research directions. 

Weaknesses: 

(1) Foundation for Claims about Orexin and Histamine Systems: The manuscript needs to provide a clearer theoretical or empirical foundation for claims regarding the impact of light on the orexin and histamine systems in the abstract. 

(2) Inclusion of Cortical Correlates: While focused on the hypothalamus, the manuscript may benefit from discussing the role of cortical activation in cognitive performance, suggesting an opportunity to expand the scope of the manuscript. 

(3) Details of Light Exposure Control: More detailed information about how light exposure was controlled and standardized is needed to ensure the replicability and validity of the experimental conditions. 

(4) Rationale Behind Different Exposure Protocols: To clarify methodological choices, the manuscript should include more in-depth reasoning behind using different protocols of light exposure for executive and emotional tasks. 

Reviewer #2 (Recommendations For The Authors): 

Attention to English language precision and correction of typographical errors, such as "hypothalamic nuclei" instead of "hypothalamus nuclei," is necessary for enhancing the manuscript.

We thank the reviewer for recognising the interest and strength of our study.

(1) As detailed in the discussion, we do believe orexin and histamine are excellent candidates for mediating the results we report. As also pointing out, however, we are in no position to know which neurons, nuclei, neurotransmitter and neuromodulator underlie the results. The last sentence of the abstract (PAGE 2) was therefore removed as we agree the statement was too strong. We carefully reconsider the discussion and believe that no such overstatement was present.

(2) Hypothalamus nuclei are connected to multiple cortical (and subcortical) structures. The relevance of these projections will vary with the cognitive task considered. In addition, we have not yet considered the cortex in our analyses such that truly integrating cortical structures appears premature. 

We nevertheless added the following short statement (PAGE 11): “Subcortical structures, and particularly those receiving direct retinal projections, including those of the hypothalamus, are likely to receive light illuminance signal first before passing on the light modulation to the cortical regions involved in the ongoing cognitive process (Campbell et al., 2023).”

(3) We now include the following as part of the method section (PAGES 16-17): “Illuminance and spectra could not be directly measured within the MRI scanner due to the ferromagnetic nature of measurement systems. The coil of the MRI and the light stand, together with the lighting system were therefore placed outside of the MR room to reproduce the experimental conditions of the in a completely dark room. A sensor was placed 2 cm away from the mirror of the coil that is mounted at eye level, i.e. where the eye of the first author of the paper would be positioned, to measure illuminance and spectra. The procedure was repeated 4 times for illuminance and twice for spectra and measurements were averaged. This procedure does not take into account interindividual variation in head size and orbit shape such that the reported illuminance levels may have varied slightly across subjects. The relative differences between illuminance are, however, very unlikely to vary substantially across participants such that statistics consisting of tests for the impact of relative differences in illuminance were not affected. The detailed values reported in Supplementary Table 2 were computed combining spectra and illuminance using the excel calculator associated with a published work (Lucas et al., 2014).”

(4) The explanation regarding the choice of the illuminance is now included in the revised manuscript (PAGE 17): “Blue-enriched light illuminances were set according to the technical characteristics of the light source and to keep the overall photon flux similar to prior 3T MRI studies of our team (between ~1012 and 1014 ph/cm²/s) (Vandewalle et al., 2010, 2011). The orange light was introduced as a control visual stimulation for potential secondary whole-brain analyses. For the present region of interest analyses, we discarded colour differences between the light conditions and only considered illuminance as indexed by mel EDI lux. This constitutes a limitation of our study as it does not allow attributing the findings to a particular photoreceptor class.”

(5) The manuscript was thoroughly rechecked, and we hope to have spotted all typos and language errors.

Reviewer #3 (Public Review): 

Summary: 

Campbell and colleagues use a combination of high-resolution fMRI, cognitive tasks, and different intensities of light illumination to test the hypothesis that the intensity of illumination differentially impacts hypothalamic substructures that, in turn, promote alterations in arousal that affect cognitive and affective performance. The authors find evidence in support of a posterior-to-anterior gradient of increased blood flow in the hypothalamus during task performance that they later relate to performance on two different tasks. The results provide an enticing link between light levels, hypothalamic activity, and cognitive/affective function, however, clarification of some methodological choices will help to improve confidence in the findings. 

Strengths: 

* The authors' focus on the hypothalamus and its relationship to light intensity is an important and understudied question in neuroscience. 

Weaknesses: 

(1) I found it challenging to relate the authors' hypotheses, which I found to be quite compelling, to the apparatus used to test the hypotheses - namely, the use of orange light vs. different light intensities; and the specific choice of the executive and emotional tasks, which differed in key features (e.g., block-related vs. event-related designs) that were orthogonal to the psychological constructs being challenged in each task. 

(4) Given the small size of the hypothalamus and the irregular size of the hypothalamic parcels, I wondered whether a more data-driven examination of the hypothalamic time series would have provided a more parsimonious test of their hypothesis. 

Reviewer #3 (Recommendations For The Authors): 

(1) The authors may wish to explain the importance of the orange light condition in the early section of the results -- i.e., when they first present the task structure. As it stands, I don't have a good appreciation of why the orange light was included -- was it a control condition? And if the differences between the light conditions (e.g., the narrow- vs. wide-band of light) were indeed ignored by focussing on the illuminance levels, are there any potential issues that the authors could then mitigate against with further experiments/analyses? 

(2) Are there other explanations for why illuminance levels might improve cognitive performance? For instance, the capacity to more easily perceive the stimuli in an experiment could plausibly make it easier to complete a given task. If this is the case, can the authors conceptualise a way to rule out this hypothesis? 

(3) Did the authors control for the differences in the number of voxels in each hypothalamic subregion? Or perhaps consider estimating the variance across voxels within the larger parcels, to determine whether the mean time series was comparable to the time series of the smaller parcels? 

(4) An alternative strategy that would mitigate against the differences in the size of hypothalamic parcels would be to conduct analyses on the hypothalamus without parcellation, but instead using dimensionality reduction techniques to observe the natural spread of responses across the hypothalamus. From the authors' results, my intuition is that these analyses will lead to similar conclusions, albeit without any of the potential issues with respect to differently-sized parcels. 

We thank the reviewer for acknowledging the originality and interest of our study. We agree that some methodological choices needed more explanation. We will address the weaknesses they pointed out as follows:

(1) The explanation regarding the choice of the illuminance is now included in the revised manuscript (PAGE 17): “Blue-enriched light illuminances were set according to the technical characteristics of the light source and to keep the overall photon flux similar to prior 3T MRI studies of our team (between ~1012 and 1014 ph/cm²/s) (Vandewalle et al., 2010, 2011). The orange light was introduced as a control visual stimulation for potential secondary whole-brain analyses. For the present region of interest analyses, we discarded colour differences between the light conditions and only considered illuminance as indexed by mel EDI lux. This constitutes a limitation of our study as it does not allow attributing the findings to a particular photoreceptor class.”

The revised discussion makes clear that these choices limit the interpretation about the photoreceptors involved (PAGE 12-13): “We based our rationale and part of our interpretations on ipRGC projections, which have been demonstrated in rodents to channel the NIF biological impact of light and incorporate the inputs from rods and cones with their intrinsic photosensitivity into a light signal that can impact the brain (Güler et al., 2008; Tri & Do, 2019). Given the polychromatic nature of the light we used, classical photoreceptors and their projections to visual brain areas are, however, very likely to have directly or indirectly contributed to the modulation by light of the regional activity of the hypothalamus.”

We further mention that (PAGE 13): “Furthermore, we cannot exclude that colour and/or spectral differences between the orange and 3 blue-enriched light conditions may have contributed to our findings. Research in rodent model demonstrated that variation in the spectral composition of light was perceived by the suprachiasmatic nucleus to set circadian timing (Walmsley et al., 2015). No such demonstration has, however, been reported yet for the acute impact of light on alertness, attention, cognition or affective state.”

Regarding the choice of tasks, we added the following the method section (PAGE 18): “Prior work of our team showed that the n-back task and emotional task included in the present protocol were successful probes to demonstrate that light illuminance modulates cognitive activity, including within subcortical structures (though resolution did not allow precise isolation of nuclei or subparts) (e.g. (Vandewalle et al., 2007, 2010)). When taking the step of ultra-high-field imaging, we therefore opted for these tasks as our goal was to show that illuminance affects brain activity across cognitive domains while not testing for task-specific aspects of these domains.”

We further added to the discussion (PAGE 8): “The pattern of light-induced changes was consistent across an executive and an emotional task which consisted of block and an event-related fMRI design, respectively. This suggests that a robust anterior-posterior gradient of activity modulation by illuminance is present in hypothalamus across cognitive domains.”

(2) We are unsure what the reviewer refers to when he states that the experiment could make it easier to perceive a stimulus. Aside from the fact that illuminance can increase alertness and attention such that a stimulus may be better or more easily perceived/processed, we do not see how blocks of ambient light, i.e. a long-lasting visual stimulus, may render auditory stimulation (letters or pseudo-words in the present) easier to perceive. To our knowledge multimodal or cross-modal integration has been robustly demonstrated for short visual/auditory cues that would precede or accompany auditory/visual stimulation. 

We are willing to clarify this issue in the text if we receive additional explanation from the reviewer.

(3) We added subpart size as covariate in the analyses (instead of subpart number) and it did not affect the output of the statistical analyses (Author response table 1). 

For completeness, we further computed standard deviation of the activity estimates of the voxels within each parcel for the main analysis of the n-back tasks and found a main effect of subpart (Author response table 2) indicating that the variability of the estimates varied across subparts. Post hoc contrast and the display included in Author response image1 show however that the difference were not related to subpart size per see. It is in fact the largest subpart (subpart 4) that shows the largest variability while one of the smallest subpart (subpart 2) shows the lowest variability. Though it may have contributed, it is therefore unlikely to explain our findings. We consider the analyses reported in (Author response table 1 and 2 and (Author response image 1 as very technical and did not include it in the supplementary material for conciseness. If the reviewer judges it essential, we can reconsider our decision.  

While computing these analyses, we realized that there were errors in the table 1 reporting the statistical outcomes of the main analyses of the emotional task. The main statistical outputs remain the same except for a nominal main effect of the task (emotional vs. neutral) and the fact that post hoc show a consistent difference between the posterior subpart (subpart 3) and all the other subparts, rather than all the other subparts except for the difference with superior tubular hypothalamus subpart: p-corrected = 0.09. We apologise for this slight error and were unable to isolate its origin. It does not modify the rest of the analyses (which were also rechecked) and the interpretations. 

Author response table 1.

Recomputations of the main GLMMs using subpart sizes rather than subpart numbers as covariate of interest.

Author response image 1.

Activity estimate variability per hypothalamus subpart and subpart size.  

Author response table 2.

Difference in activity estimate standard deviation between hypothalamus subparts during the n-back task.

Outputs of the generalized linear mixed model (GLMM) with subject as the random factor (intercept and slope), and task and subpart as repeated measures (ar(1) autocorrelation).

* The corrected p-value for multiple comparisons over 2 tests is p < 0.025.

# Refer to Fig.2A for correspondence of subpart numbers

The text referring to Table 1 was modified accordingly (PAGE 5): “A nominal main effect of the task was detected for the emotional task [p = 0.049; Table 1] but not for the n-back task. For both tasks, there was no significant main effect for any of the other covariates and post hoc analyses showed that the index of the illuminance impact was consistently different in the posterior hypothalamus subpart compared to the other subparts [pcorrected ≤ 0.05]”.

(4) We agree that a data driven approach could have constituted an alternative means to tests our hypothesis. We opted for an approach that we mastered best, while still allowing to conclusively test for regional differences in activity across the hypothalamus. Examination of time series of the very same data we used will mainly confirm the results of our analyses – an anterior-posterior gradient in the impact of illuminance - while it may yield slight differences in the boarders of the subparts of the hypothalamus undergoing decreased or increased activity with increasing illuminance. While the suggested approach may have been envisaged if we had been facing negative results (i.e. no differences between subparts, potentially because subparts would not reflect functional differences in response to illuminance change), it would constitute a circular confirmation of our main findings (i.e. using the same data). While we truly appreciate the suggestion, we do not consider that it would constitute a more parsimonious test of our hypothesis, now that we successfully applied GLM/parcellation and GLMM approaches.

We added the following statement to the discussion to take this comment into account (PAGE 12): “Future research may consider data-driven analyses of hypothalamus voxels time series as an alternative to the parcellation approach we adopted here. This may refine the delineation of the subparts of the hypothalamus undergoing decreased or increased activity with increasing illuminance.”

Response references

Albers, H. E., Walton, J. C., Gamble, K. L., McNeill, J. K., & Hummer, D. L. (2017). The dynamics of GABA signaling: Revelations from the circadian pacemaker in the suprachiasmatic nucleus. Frontiers in Neuroendocrinology, 44, 35–82. https://doi.org/10.1016/J.YFRNE.2016.11.003

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Author response:

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

Public Reviews:

Reviewer #1 (Public review):

This paper examines the role of MLCK (myosin light chain kinase) and MLCP (myosin light chain phosphatase) in axon regeneration. Using loss-of-function approaches based on small molecule inhibitors and siRNA knockdown, the authors explore axon regeneration in cell culture and in animal models. Their evidence shows that MLCK activity facilitates axon extension/regeneration, while MLCP prevents it.

Major concern:

A global inconsistency in the conclusions of the authors is evident when trying to understand the role of NMII in axon growth and to understand the present results in light of previous reports by the authors and many others on the role of NMII in axon extension. The discussion of the matter fails to acknowledge a vast literature on how NMII activity is regulated. The authors study enzymes responsible for the phosphorylation and dephosphorylation of NMII, referring to something that is strongly proven elsewhere, that phosphorylation activates NMII and dephosphorylation deactivates it. The authors mention their own previous evidence using inhibitors of NMII ATPase activity (blebbistatin, Bleb for short) and inhibitors of a kinase that phosphorylates NMII (ROCK), highlighting that Bleb increases axon growth. Since Bleb inhibits the ATPase activity of NMII, it follows that NMII is in itself an inhibitor of axon growth, and hence when NMII is inhibited, the inhibition on axon growth is relieved, and axonal growth takes place (REF1). It is known that NMII exists in an inactive folded state, and ser19 phosphorylation (by MLCK or ROCK) extends the protein, allowing NMII filament formation, ATPase activity, and force generation on actin filaments (REF2). From this, it is derived that if MLCK is inhibited, then there is no NMII phosphorylation, and hence no NMII activity, and, according to their previous work, this should promote axon growth. On the contrary, the authors show the opposite effect: in the lack of phospho-MLC, authors show axon growth inhibition.

We thank the Reviewer for taking time to review our manuscript, and we really appreciated the comments from the reviewer. We have tried our best to revise the manuscript to address all the comments raised by the Reviewer.

Reporting evidence challenging previous conclusions is common business in scientific endeavors, but the problem with the current manuscript is that it fails to point to and appropriately discuss this contradiction. Instead, the authors refer to the fact that MLCK and Bleb inhibit NMII in different steps of the activation process. While this is true, this explanation does not solve the contradiction. There are many options to accommodate the information, but it is not the purpose of this revision to provide them. Since the manuscript is focused solely on phosphorylation states of MLC and axon extension, the claims are simply at odds with the current literature, and this important finding, if true, is not properly discussed.

Thank you for reviewer's very good comments. As suggested by Reviewer, we discuss more detail it in our revised manuscripts (line 357-368; line 373-374).

What follows is a discussion of the merits and limitations of different claims of the manuscript in light of the evidence presented.

(1) Using western blot and immunohistochemical analyses, authors first show that MLCK expression is increased in DRG sensory neurons following peripheral axotomy, concomitant to an increase in MLC phosphorylation, suggesting a causal effect (Figure 1). The authors claim that it is common that axon growth-promoting genes are upregulated. It would have been interesting at this point to study in this scenario the regulation of MLCP, which is a main subject in this work, and expect its downregulation.

We thank the Reviewer for taking time to review our manuscript, and we really appreciated the positive comments from the Reviewer.

(2) Using DRG cultures and sciatic nerve crush in the context of MLCK inhibition and down-regulation, authors conclude that MLCK activity is required for mammalian peripheral axon regeneration both in vitro and in vivo (Figure 2).

The in vitro evidence is of standard methods and convincing. However, here, as well as in all other experiments using siRNAs, it is not clear what the control is about (the identity of the plasmids and sequences, if any).

We used the pCMV–EGFP–N3 as control, and the pCMV–EGFP–N3 plasmid was from Clontech, Inc. (line 114-115).   

Related to this, it is not helpful to show the same exact picture as a control example in Figures 2 and 3 (panels J and E, respectively). Either because they should not have received the same control treatment, or simply because it raises concern that there are no other control examples worth showing. In these images, it is not also clear where and how the crush site is determined in the GFP channel. This is of major importance since the axonal length is measured from the presumed crush site. Apart from providing further details in the text, the authors should include convincing images.

Thank you so much for your comments. We changed the control example in Figure 3J. For sciatic nerve regeneration experiments, the sciatic nerve was exposed at the sciatic notch by a small incision 2 days after the in vivo electroporation. The nerve was then crushed, and the crush site was marked with a 11-0 nylon epineural suture. After surgeries, the wound was closed, and the mice were allowed to recover. Three days after the sciatic nerve crush, the whole sciatic nerves from the perfused animals were dissected out and postfixed overnight in 4% PFA at 4°C. Before whole-mount flattening, it was confirmed that the place of epineural suture matched the injury site, and experiments were included in the analysis only when the crush site was clearly identifiable. Using whole mounted tissue, all identifiable EGFP-labeled axons in the sciatic nerve were manually traced from the crush site to the distal growth cone to measure the length of axon regeneration. (line 159-164).

(3) The authors then examined the role of the phosphatase MLCP in axon growth during regeneration. The authors first use a known MLCP blocker, phorbol 12,13-dibutyrate (PDBu), to show that is able to increase the levels of p-MLC, with a concomitant increase in the extent of axon regrowth of DRG neurons, both in permissive as well as non-permissive. The authors repeat the experiments using the knockdown of MYPT1, a key component of the MLC-phosphatase, and again can observe a growth-promoting effect (Figure 3).

The authors further show evidence for the growth-enhancing effect in vivo, in nerve crush experiments. The evidence in vivo deserves more evidence and experimental details (see comment 2). Some key weaknesses of the data were mentioned previously (unclear RNAi controls and duplication of shown images), but in this case, it is also not clear if there is a change only in the extent of growth, or also in the number of axons that are able to regenerate.

Thank you so much for your comments. We used same control as in vitro experiments (the pCMV– EGFP–N3 plasmid was from Clontech, Inc), and we also changed the control image in Figure 3J. For in vivo axon regeneration experiments, we measured the lengths of all identifiable EGFP-labelled axons in the sciatic nerve from the crush site to the distal axonal ends. The number of EGFP labeled regenerating axons were actually determined by the electroporation rate of EGFP, which is similar, but not identical, in different mice. Thus, our data only can show the differences in axon lengths among different experimental conditions. Such approach has been used in many of our previously published papers (e.g. Saijilafu et al. Nature Communications, 2011, Saijilafu et al. Nature Communications, 2013). (line 152-153).

(4) In the next set of experiments (presented in Figure 4) authors extend the previous observations in primary cultures from the CNS. For that, they use cortical and hippocampal cultures, and pharmacological and genetic loss-of-function using the above-mentioned strategies. The expected results were obtained in both CNS neurons: inhibition or knockdown of the kinase decreases axon growth, whereas inhibition or knockdown of the phosphatase increases growth. A main weakness in this set is that it is not indicated when (at what day in vitro, DIV) the treatments are performed. This is important to correctly interpret the results, since in the first days in vitro these neurons follow well-characterized stages of development, with characteristic cellular events with relevance to what is being evaluated. Importantly, this would be of value to understand whether the treatments affect axonal specification and/or axonal extension. Although these events are correlated, they imply a different set of molecular events.

The treatments were started from the initial of cell culture period, and this procedure may affect axon specification as the Reviewer point out. However, we mainly focused on axon length in our experiments, thus, for quantification of axon length, neurons with processes longer than twice the diameter of cell bodies were photographed, and the longest axon of each neuron was measured. We revised the manuscript as suggested by the reviewer (line 143-145).

The title of this section is misleading: line 241 "MLCK/MLCP activity regulated axon growth in the embryonic CNS"... the title (and the conclusion) implies that the experiments were performed in situ, looking at axons in the developing brain. The most accurate title and conclusion should mention that the evidence was collected in CNS primary cultures derived from embryos.

We have revised the manuscript as suggested by the reviewer (line 251).

(5) Performing nerve crush injury in CNS nerves (optic nerve and spinal cord), and the local application of PBDu, the author shows contrasting results (Figure 5). In the ON nerve, they can see axons extending beyond the lesion site due to PBDu. On the contrary, the authors fail to observe so in the corticospinal tract present in the spinal cord. The authors fail to discuss this matter in detail. Also, they accommodate the interpretation of the evidence in light of a process known as axon retraction, and its prevention by MLCP inhibition. Since the whole paper is on axon extension, and it is known that mechanistically axon retraction is not merely the opposite of axon extension, the claim needs far more evidence.

Thank you so much for your comments. Compared to optic nerve axons, corticospinal tract axons exhibit a reduced intrinsic axon growth capability. Consequently, we observed that PBDu stimulates optic nerve axon regeneration. However, unfortunately, we did not detect any enhancement in corticospinal tract axons beyond the injury site in SCI following the inhibition of myosin light chain phosphatase (MLCP) with PBDu.

In panel 5F and the supplementary data, the authors mention the occurrence of retraction bulbs, but the images are too small to support the claim, and it is not clear how these numbers were normalized to the number of axons labeled in each condition.

Thank you so much for your comments. In this study, we used a similar method from Ertürk et al. (2007) to quantify the retraction bulb. Both maximum width of the enlarged distal tip of the axon and the width of its immediately adjacent axon shaft was measured. Then, the ratio of these two widths was then calculated. An axonal tip was considered as a retraction bulb if its tip/shaft ratio exceeded 4. Averages number of retraction bulb were calculated from 3 sections in every mice for each group (n=5). (line 187-191).

[Ref] Ertürk A, Hellal F, Enes J, and Bradke F (2007). Disorganized microtubules underlie the formation of retraction bulbs and the failure of axonal regeneration. J. Neurosci 27, 9169–9180. [PubMed:17715353].

(6) The author combines MLCK and MLCP inhibitors with Bleb, trying to verify if both pairs of inhibitors act on the same target/pathway (Figure 6). The rationale is wrong for at least two reasons.<br /> a- Because both lines of evidence point to contrasting actions of NMII on axon growth, one approach could never "rescue" the other.

If MLCK regulates axon growth through the activation of Myosin, the inhibitory effect of ML-7 (an MLCK inhibitor) on axon growth might be influenced by Bleb, a NMII inhibitor. However, our findings reveal that the combination of Bleb and ML-7 does not alter the rate of axon outgrowth compared to ML-7 alone. This suggests that the roles of ML-7 and Bleb in axon growth are independent. It means MLCK may regulates axon growth independent of NMII activity.

b. Because the approaches target different steps on NMII activation, one could never "prevent" or rescue the other. For example, for Bleb to provide a phenotype, it should find any p-MLC, because it is only that form of MLC that is capable of inhibiting its ATPase site. In light of this, it is not surprising that Bleb is unable to exert any action in a situation where there is no p-MLC (ML-7, which by inhibiting the kinase drives the levels of p-MLC to zero, Figure 4A). Hence, the results are not possible to validate in the current general interpretation of the authors. (See 'major concern').

The reported mechanism of blebbistatin is not through competition with the ATP binding site of myosin. Instead, it selectively binds to the ATPase intermediate state associated with ADP and inorganic phosphate, which decelerates the phosphate release. Importantly, blebbistatin does not impede myosin's interaction with actin or the ATP-triggered disassociation of actomyosin. It rather inhibits the myosin head when it forms a product complex with a reduced affinity for actin. This indicates that blebbistatin functions by stabilizing a particular myosin intermediate state that is independent of the phosphorylation status of myosin light chain (MLC).

[Ref] Kovács M, Tóth J et al. Mechanism of blebbistatin inhibition of myosin II. J Biol Chem. 2004 Aug 20;279(34):35557-63. doi: 10.1074/jbc.M405319200.

(7) In Figure 7, the authors argue that the scheme of replating and using ML7 before or after replating is evidence for a local cytoskeletal action of the drug. However, an alternative simpler explanation is that the drug acts acutely on its target, and that, as such, does not "survive" the replating procedure. Hence, the conclusion raised by the evidence shown is not supported.

In our study, we meticulously assessed the neuronal survival rates across various experimental groups. The findings indicate no significant variation in survival rates among the groups. This suggests that the drug treatment exerts no discernible influence on cell viability but primarily modulates axonal elongation."

Author response image 1.

(8) In Figure 8, the authors show that the inhibitory treatments on MLCK and MLCP (ML7 and PRBu) alter the morphology of growth cones. However, it is not clear how this is correlated with axon growth. The authors also mention in various parts of the text that a local change in the growth cone is evidence for a local action/activity of the drug or enzyme. However, the local change<->local action is not a logical truth. It can well be that MLCK and MLCP activity trigger molecular events that ultimately have an effect elsewhere, and by looking at "elsewhere" one observes of course a local effect but is not because the direct action of MLCK or MLCP are localized. To prove true localized effects there are numerous efforts that can be made, starting from live imaging, fluorescent sensors, and compartmentalized cultures, just to mention a few.

About the relationship between growth cone size and its growth rate, the previous published literatures found that a fast-growing axon tended to have small growth cones (Mason C. et al. 1997). A recent study on Aplysia further supports this by noting that growth cones enlarge significantly when axonal elongation halts (Miller and Suter, 2018). Consistent with these findings, our data indicate that inhibiting MLCP with PDBu treatment leads to a reduction in growth cone size, which in turn promotes axon regeneration.

[Ref] Mason CA, Wang LC. Growth cone form is behavior-specific and, consequently, position-specific along the retinal axon pathway. J Neurosci. 1997; 13:1086–1100. [PubMed: 8994063]

[Ref] Miller KE, Suter DM. An Integrated Cytoskeletal Model of Neurite Outgrowth. Front Cell Neurosci. 2018 Nov 26;12:447. doi: 10.3389/fncel.2018.00447. eCollection 2018.

References:

(1) Eun-Mi Hur 1, In Hong Yang, Deok-Ho Kim, Justin Byun, Saijilafu, Wen-Lin Xu, Philip R Nicovich, Raymond Cheong, Andre Levchenko, Nitish Thakor, Feng-Quan Zhou. 2011. Engineering neuronal growth cones to promote axon regeneration over inhibitory molecules. Proc Natl Acad Sci U S A. 2011 Mar 22;108(12):5057-62. doi: 10.1073/pnas.1011258108.

(2) Garrido-Casado M, Asensio-Juárez G, Talayero VC, Vicente-Manzanares M. 2024. Engines of change: Nonmuscle myosin II in mechanobiology. Curr Opin Cell Biol. 2024 Apr;87:102344. doi: 10.1016/j.ceb.2024.102344.

(3) Karen A Newell-Litwa 1, Rick Horwitz 2, Marcelo L Lamers. 2015. Non-muscle myosin II in disease: mechanisms and therapeutic opportunities. Dis Model Mech. 2015 Dec;8(12):1495-515. doi: 10.1242/dmm.022103.

Reviewer #2 (Public review):

Summary:

Saijilafu et al. demonstrate that MLCK/MLCP proteins promote axonal regeneration in both the central nervous system (CNS) and peripheral nervous system (PNS) using primary cultures of adult DRG neurons, hippocampal and cortical neurons, as well as in vivo experiments involving sciatic nerve injury, spinal cord injury, and optic nerve crush. The authors show that axon regrowth is possible across different contexts through genetic and pharmacological manipulation of these proteins. Additionally, they propose that MLCK/MLCP may regulate F-actin reorganization in the growth cone, which is significant as it suggests a novel strategy for promoting axonal regeneration.

Strengths:

This manuscript presents a comprehensive array of experimental models, addressing the biological question in a broad manner. Particularly noteworthy is the use of multiple in vivo models, which significantly strengthens the overall validity of the study.

We thank the Reviewer for taking time to review our manuscript, and we really appreciated the positive comments from the Reviewer.

Weaknesses:

The following aspects apply:

(1) The manuscript initially references prior research by the authors suggesting that NMII inhibition enhances axonal growth and that MLCK activates NMII. However, the study introduces a contradiction by demonstrating that MLCK inhibition (via ML-7 or siMLCK) inhibits axonal growth. This inconsistency is not adequately addressed or discussed in the manuscript.

Thank you for reviewer's very good comments. As suggested by Reviewer, we discuss more detail it in our revised manuscripts (line 357-368; line373-374).

(2) While the study proposes that MLCK/MLCP regulates F-actin redistribution in the growth cone, the mechanism is not explored in depth. The only figure showing how pharmacological manipulation affects the growth cone suggests that not only F-actin but also the microtubule cytoskeleton might be affected, indicating that the mechanism may not be specific. A deeper exploration of this relationship in DRG neurons, in addition to cortical neurons, as shown in the study, would be beneficial.

Thank you for your insightful suggestion. However, our study primarily focuses on actin and myosin dynamics in the context of axonal elongation, as indicated by our direct observations in growing dorsal root ganglia (DRGs). Athamneh et al. (2017) elegantly demonstrated that the bulk movement of microtubules (MTs), rather than their assembly, predominantly drives MT advance during axonal elongation. Consequently, our manuscript concentrates on the actomyosin system, which is central to our findings. While the role of MTs in axonal growth is indeed significant and fascinating, the data we present is predominantly concerned with the actomyosin mechanism.

[Ref] Athamneh, A. I. M. et al. Neurite elongation is highly correlated with bulk forward translocation of microtubules. Scientific Reports 7, (2017).

(3) In the sciatic nerve injury experiments, it would be crucial to include additional controls that clearly demonstrate that siMYPT1 treatment increases MLCP in the L4-L5 ganglia. Additionally, although the manuscript mentions quantifying axons expressing EGFP, the Materials and Methods section only discusses siMYPT1 electroporation, which could lead to confusion.

Thank you for your suggestion. However, due to the unavailability of a suitable commercial MLCP antibody, we were unable to directly detect MLCP expression. Instead, we assessed the phosphorylation level of myosin light chain (MLC) as a proxy to indicate that siMYPT1 transfection effectively downregulates MLCP activity in L4/5 dorsal root ganglia (DRG). This approach was taken to ensure the integrity of our findings despite the limitations in antibody availability.

About the electroporation method section, we have now included detailed information about the control plasmid used in our experiments to ensure a clear understanding of our experimental setup and to validate our results. A 1 μl solution containing indicated siRNAs together with the plasmid encoding EGFP (pCMV–EGFP–N3) was then microinjected into the L4–L5 DRG….. (line 152-153).

(4) In some panels, it is difficult to differentiate the somas from the background (Figures 3, 4, 7). In conditions where images with shorter axonal lengths are represented, it is unclear whether this is due to fewer cells or reduced axonal growth (Figures 2, 4, 6).

In the original submission, there was some loss of image quality while converting the TIFF to PDF. We improved the quality of images in our revised manuscripts.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

There are a number of typos and language errors that should be thoroughly revised. For example, line 219: "It is well known that the opposite role of MLCK and MLCP to regulate the MLC phosphorylation status". The term "opposite role" is vague. Using "opposite roles" and specifying that they are in regulating MLC phosphorylation status clarifies the relationship between MLCK and MLCP. Also, the original phrase "to regulate" was not correctly integrated into the sentence. Rephrasing it to "in regulating" makes the role of MLCK and MLCP clearer.

We have revised the manuscript as suggested by the reviewer (line 229).

In the same line, there is a high number of panels that are not referred to in the text or references for panels that have another letter. Just to mention a few:

- line 199: "(Figure 1F, G)", → BUT figure 1 contains no G panel.

We have revised the manuscript as suggested by the reviewer (line 209).

- line 203: "The results showed that ML-7 administration led to a significant reduction in MLC phosphorylation levels (Figure 2A, B) and impaired axonal growth in sensory neurons (Figure 2C, D). → BUT panel C is related to A and B, and only D and E show impaired axonal growth.

We have revised the manuscript as suggested by the reviewer (line 214; line 215; line 217; line 219 ).

Reviewer #2 (Recommendations for the authors):

(1) Improving the quality of the images would significantly strengthen the results presented.

In the original submission, there was some loss of image quality while converting the TIFF to PDF. We improved the quality of images in our revised manuscripts.

(2) The representative images of controls do not always show the same number of cells or axonal growth (e.g., Figure 4).

We have changed some images as suggested by the reviewer.

(3) The text has citation errors when referring to the figure labels.

Upon thorough review, we have carefully examined our manuscript and have made the necessary corrections to address the identified errors. We appreciate the opportunity to enhance the quality of our work and believe that these revisions have significantly improved the clarity of our manuscript.

(4) What happens to MLCK levels when MLCP activity is inhibited in the optic nerve?

Upon analyzing our experimental data, we observed no significant alterations in the protein levels of MLCK when the activity of MLCP was inhibited. This finding suggests that the regulatory mechanisms governing MLCK expression may not be directly influenced by short-term MLCP inhibition. It is plausible that the duration of the inhibition period was insufficient to elicit a detectable change in MLCK expression levels.

(5) The text in line 266: "In contrast, local PBS administration at the injury site or intravitreal PDBu injection induced little axon regeneration beyond the injury site (Figure 5 A-C)." However, this is not reflected in the figure.

In our revised manuscript, we have provided a more precise description of our findings: In contrast, local PBS administration at the injury site or intravitreal PDBu injection did not significantly enhance axon regeneration beyond the injury site (Figure 5 A-C). This observation suggests that the only treatment employed in the injury site (the inhibition of MLCP activity within the growth cone) effective promote axonal growth. (line 276-279).

(6) Line 287: The phrase "Consistent with our previous study" requires a citation to support it.

We added the reference paper; Consistent with our previous study 1, the inhibition of myosin II activity with 25 μM blebbistatin markedly promoted axonal growth (Figure 6A, B). (line 298)

(7) Line 333: The paper cited by Yu P et al. (2012) does not mention MLCK or p-MLC, so it appears to be misquoted.

Thank you for comments. We rechecked this cited paper and confirmed that the author provided the western data C in the supplementary figure 1, it showed that Bleb did not alter the phosphorylation status of MLC.

Author response:

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

We thank the reviewers and editors for their careful read of our paper, and appreciate the thoughtful comments.

Both reviewers agreed that our work had several major strengths: the large dataset collected in collaboration across ten labs, the streamlined processing pipelines, the release of code repositories, the multi-task neural network, and that we definitively determined that electrode placement is an important source of variability between datasets.

However, a number of key potential improvements were noted: the reviewers felt that a more standard model-based characterization of single neuron responses would benefit our reproducibility analysis, that more detail was needed about the number of cells, sessions, and animals, and that more information was needed to allow users to deploy the RIGOR standards and to understand their relationship to other metrics in the field.

We agree with these suggestions and have implemented many major updates in our revised manuscript. Some highlights include:

(1)  A new regression analysis that specifies the response profile of each neuron, allowing a comparison of how similar these are across labs and areas (See Figure 7 in the new section, “Single neuron coefficients from a regression-based analysis are rep oducible across labs”);

(2) A new decoding analysis (See Figure 9 in the section, “Decodability of task variables is consistent across labs, but varies by brain region”);

(3) A new RIGOR notebook to ease useability;

(4) A wealth of additional information about the cells, animals and sessions in each figure;

(5) Many new additional figure panels in the main text and supplementary material to clarify the specific points raised by the reviewers.

Again, we are grateful to the reviewers and editors for their helpful comments, which have significantly improved the work. We are hopeful that the many revisions we have implemented will be sufficient to change the “incomplete” designation that was originally assigned to the manuscript.

Reviewer #1 (Public review):

Summary:

The authors explore a large-scale electrophysiological dataset collected in 10 labs while mice performed the same behavioral task, and aim to establish guidelines to aid reproducibility of results collected across labs. They introduce a series of metrics for quality control of electrophysiological data and show that histological verification of recording sites is important for interpreting findings across labs and should be reported in addition to planned coordinates. Furthermore, the authors suggest that although basic electrophysiology features were comparable across labs, task modulation of single neurons can be variable, particularly for some brain regions. The authors then use a multi-task neural network model to examine how neural dynamics relate to multiple interacting task- and experimenter-related variables, and find that lab-specific differences contribute little to the variance observed. Therefore, analysis approaches that account for correlated behavioral variables are important for establishing reproducible results when working with electrophysiological data from animals performing decision-making tasks. This paper is very well-motivated and needed. However, what is missing is a direct comparison of task modulation of neurons across labs using standard analysis practice in the fields, such as generalized linear model (GLM). This can potentially clarify how much behavioral variance contributes to the neural variance across labs; and more accurately estimate the scale of the issues of reproducibility in behavioral systems neuroscience, where conclusions often depend on these standard analysis methods.

We fully agree that a comparison of task-modulation across labs is essential. To address this, we have performed two new analyses and added new corresponding figures to the main text (Figures 7 and 9). As the reviewer hoped, this analysis did indeed clarify how much behavioral variance contributes to the variance across labs. Critically, these analyses suggested that our results were more robust to reproducibility than the more traditional analyses would indicate.

Additional details are provided below (See detailed response to R1P1b).

Strengths:

(1) This is a well-motivated paper that addresses the critical question of reproducibility in behavioural systems neuroscience. The authors should be commended for their efforts.

(2) A key strength of this study comes from the large dataset collected in collaboration across ten labs. This allows the authors to assess lab-to-lab reproducibility of electrophysiological data in mice performing the same decision-making task.

(3) The authors' attempt to streamline preprocessing pipelines and quality metrics is highly relevant in a field that is collecting increasingly large-scale datasets where automation of these steps is increasingly needed.

(4) Another major strength is the release of code repositories to streamline preprocessing pipelines across labs collecting electrophysiological data.

(5) Finally, the application of MTNN for characterizing functional modulation of neurons, although not yet widely used in systems neuroscience, seems to have several advantages over traditional methods.

Thanks very much for noting these strengths of our work.

Weaknesses:

(1) In several places the assumptions about standard practices in the field, including preprocessing and analyses of electrophysiology data, seem to be inaccurately presented:

a) The estimation of how much the histologically verified recording location differs from the intended recording location is valuable information. Importantly, this paper provides citable evidence for why that is important. However, histological verification of recording sites is standard practice in the field, even if not all studies report them. Although we appreciate the authors' effort to further motivate this practice, the current description in the paper may give readers outside the field a false impression of the level of rigor in the field.

We agree that labs typically do perform histological verification. Still, our methods offer a substantial improvement over standard practice, and this was critical in allowing us to identify errors in targeting. For instance, we used new software, LASAGNA, which is an innovation over the traditional, more informal approach to localizing recording sites. Second, the requirement that two independent reviewers concur on each proposed location for a recording site is also an improvement over standard practice. Importantly, these reviewers use electrophysiological features to more precisely localize electrodes, when needed, which is an improvement over many labs. Finally, most labs use standard 2D atlases to identify recording location (a traditional approach); our use of a 3D atlas and a modern image registration pipeline has improved the accuracy of identifying the true placement of probes in 3D space.

Importantly, we don’t necessarily advocate that all labs adopt our pipeline; indeed, this would be infeasible for many labs. Instead, our hope is that the variability in probe trajectory that we uncovered will be taken into account in future studies. Here are 3 example ways in which that could happen. First, groups hoping to target a small area for an experiment might elect to use a larger cohort than previously planned, knowing that some insertions will miss their target. Second, our observation that some targeting error arose because experimenters had to move probes due to blood vessels will impact future surgeries: when an experimenter realizes that a blood vessel is in the way, they might still re-position the probe, but they can also adjust its trajectory (e.g., changing the angle) knowing that even little nudges to avoid blood vessels can have a large impact on the resulting insertion trajectory. Third, our observation of a 7 degree deviation between stereotaxic coordinates and Allen Institute coordinates can be used for future trajectory planning steps to improve accuracy of placement. Uncovering this deviation required many insertions and our standardized pipeline, but now that it is known, it can be easily corrected without needing such a pipeline.

We thank the reviewer for bringing up this issue and have added new text (and modified existing text) in the Discussion to highlight the innovations we introduced that allowed us to carefully quantify probe trajectory across labs (lines 500 - 515):

“Our ability to detect targeting error benefited from an automated histological pipeline combined with alignment and tracing that required agreement between multiple users, an approach that greatly exceeds the histological analyses done by most individual labs. Our approach, which enables scalability and standardization across labs while minimizing subjective variability, revealed that much of the variance in targeting was due to the probe entry positions at the brain surface, which were randomly displaced across the dataset. … Detecting this offset relied on a large cohort size and an automated histological pipeline, but now that we have identified the offset, it can be easily accounted for by any lab. Specifically, probe angles must be carefully computed from the CCF, as the CCF and stereotaxic coordinate systems do not define the same coronal plane angle. Minimizing variance in probe targeting is another important element in increasing reproducibility, as slight deviations in probe entry position and angle can lead to samples from different populations of neurons. Collecting structural MRI data in advance of implantation could reduce targeting error, although this is infeasible for most labs. A more feasible solution is to rely on stereotaxic coordinates but account for the inevitable off-target measurements by increasing cohort sizes and adjusting probe angles when blood vessels obscure the desired location.”

b) When identifying which and how neurons encode particular aspects of stimuli or behaviour in behaving animals (when variables are correlated by the nature of the animals behaviour), it has become the standard in behavioral systems neuroscience to use GLMs - indeed many labs participating in the IBL also has a long history of doing this (e.g., Steinmetz et al., 2019; Musall et al., 2023; Orsolic et al., 2021; Park et al., 2014). The reproducibility of results when using GLMs is never explicitly shown, but the supplementary figures to Figure 7 indicate that results may be reproducible across labs when using GLMs (as it has similar prediction performance to the MTNN). This should be introduced as the first analysis method used in a new dedicated figure (i.e., following Figure 3 and showing results of analyses similar to what was shown for the MTNN in Figure 7). This will help put into perspective the degree of reproducibility issues the field is facing when analyzing with appropriate and common methods. The authors can then go on to show how simpler approaches (currently in Figures 4 and 5) - not accounting for a lot of uncontrolled variabilities when working with behaving animals - may cause reproducibility issues.

We fully agree with the reviewer's suggestion. We have addressed their concern by implementing a Reduced-Rank Regression (RRR) model, which builds upon and extends the principles of Generalized Linear Models (GLMs). The RRR model retains the core regression framework of GLMs while introducing shared, trainable temporal bases across neurons, enhancing the model’s capacity to capture the structure in neural activity (Posani, Wang, et al., bioRxiv, 2024). Importantly, Posani, Wang et al compared the predictive performance of GLMs vs the RRR model, and found that the RRR model provided (slightly) improved performance, so we chose the RRR approach here.

We highlight this analysis in a new section (lines 350-377) titled, “Single neuron coefficients from a regression-based analysis are reproducible across labs”. This section includes an entirely new Figure (Fig. 7), where this new analysis felt most appropriate, since it is closer in spirit to the MTNN analysis that follows (rather than as a new Figure 3, as the reviewer suggested). As the reviewer hoped, this analysis provides some reassurance that including many variables when characterizing neural activity furnishes results with improved reproducibility. We now state this in the Results and the Discussion (line 456-457), highlighting that these analyses complement the more traditional selectivity analyses, and that using both methods together can be informative.

When the authors introduce a neural network approach (i.e. MTNN) as an alternative to the analyses in Figures 4 and 5, they suggest: 'generalized linear models (GLMs) are likely too inflexible to capture the nonlinear contributions that many of these variables, including lab identity and spatial positions of neurons, might make to neural activity'). This is despite the comparison between MTNN and GLM prediction performance (Supplement 1 to Figure 7) showing that the MTNN is only slightly better at predicting neural activity compared to standard GLMs. The introduction of new models to capture neural variability is always welcome, but the conclusion that standard analyses in the field are not reproducible can be unfair unless directly compared to GLMs.

In essence, it is really useful to demonstrate how different analysis methods and preprocessing approaches affect reproducibility. But the authors should highlight what is actually standard in the field, and then provide suggestions to improve from there.

Thanks again for these comments. We have also edited the MTNN section slightly to accommodate the addition of the previous new RRR section (line 401-402).

(2) The authors attempt to establish a series of new quality control metrics for the inclusion of recordings and single units. This is much needed, with the goal to standardize unit inclusion across labs that bypasses the manual process while keeping the nuances from manual curation. However, the authors should benchmark these metrics to other automated metrics and to manual curation, which is still a gold standard in the field. The authors did this for whole-session assessment but not for individual clusters. If the authors can find metrics that capture agreed-upon manual cluster labels, without the need for manual intervention, that would be extremely helpful for the field.

We thank the reviewer for their insightful suggestions regarding benchmarking our quality control metrics against manual curation and other automated methods at the level of individual clusters. We are indeed, as the reviewer notes, publishing results from spike sorting outputs that have been automatically but not manually verified on a neuron-by-neuron basis. To get to the point where we trust these results to be of publishable quality, we manually reviewed hundreds of recordings and thousands of neurons, refining both the preprocessing pipeline and the single-unit quality metrics along the way. All clusters, both those passing QCs and those not passing QCs, are available to review with detailed plots and quantifications at https://viz.internationalbrainlab.org/app (turn on “show advanced metrics” in the upper right, and navigate to the plots furthest down the page, which are at the individual unit level). We would emphasize that these metrics are definitely imperfect (and fully-automated spike sorting remains a work in progress), but so is manual clustering. Our fully automated approach has the advantage of being fully reproducible, which is absolutely critical for the analyses in the present paper. Indeed, if we had actually done manual clustering or curation, one would wonder whether our results were actually reproducible independently. Nevertheless, it is not part of the present manuscript’s objectives to validate or defend these specific choices for automated metrics, which have been described in detail elsewhere (see our Spike Sorting whitepaper, https://figshare.com/articles/online_resource/Spike_sorting_pipeline_for_the_International_Brain_La boratory/19705522?file=49783080). It would be a valuable exercise to thoroughly compare these metrics against a careful, large, manually-curated set, but doing this properly would be a paper in itself and is beyond the scope of the current paper. We also acknowledge that our analyses studying reproducibility across labs could, in principle, result in more or less reproducibility under a different choice of metrics, which we now describe in the Discussion (line 469-470)”:

“Another significant limitation of the analysis presented here is that we have not been able to assess the extent to which other choices of quality metrics and inclusion criteria might have led to greater or lesser reproducibility.”

(3) With the goal of improving reproducibility and providing new guidelines for standard practice for data analysis, the authors should report of n of cells, sessions, and animals used in plots and analyses throughout the paper to aid both understanding of the variability in the plots - but also to set a good example.

We wholeheartedly agree and have added the number of cells, mice and sessions for each figure. This information is included as new tabs in our quality control spreadsheet (https://docs.google.com/spreadsheets/d/1_bJLDG0HNLFx3SOb4GxLxL52H4R2uPRcpUlIw6n4 n-E/). This is referred to in line 158-159 (as well as its original location on line 554 in the section, “Quality control and data inclusion”).

Other general comments:

(1) In the discussion (line 383) the authors conclude: 'This is reassuring, but points to the need for large sample sizes of neurons to overcome the inherent variability of single neuron recording'. - Based on what is presented in this paper we would rather say that their results suggest that appropriate analytical choices are needed to ensure reproducibility, rather than large datasets - and they need to show whether using standard GLMs actually allows for reproducible results.

Thanks. The new GLM-style RRR analysis in Figure 7, following the reviewer’s suggestion, does indeed indicate improved reproducibility across labs. As described above, we see this new analysis as complementary to more traditional analyses of neural selectivity and argue that the two can be used together. The new text (line 461) states:

“This is reassuring, and points to the need for appropriate analytical choices to ensure reproducibility.”

(2) A general assumption in the across-lab reproducibility questions in the paper relies on intralab variability vs across-lab variability. An alternative measure that may better reflect experimental noise is across-researcher variability, as well as the amount of experimenter experience (if the latter is a factor, it could suggest researchers may need more training before collecting data for publication). The authors state in the discussion that this is not possible. But maybe certain measures can be used to assess this (e.g. years of conducting surgeries/ephys recordings etc)?

We agree that understanding experimenter-to-experimenter variability would be very interesting and indeed we had hoped to do this analysis for some time. The problem is that typically, each lab employed one trainee to conduct all the data collection. This prevents us from comparing outcomes from two different experimenters in the same lab. There are exceptions to this, such as the Churchland lab in which 3 personnel (two postdocs and a technician) collected the data. However, even this fortuitous situation did not lend itself well to assessing experimenter-to-experimenter variation: the Churchland lab moved from Cold Spring Harbor to UCLA during the data collection period, which might have caused variability that is totally independent of experimenter (e.g., different animal facilities). Further, once at UCLA, the postdoc and technician worked closely together- alternating roles in animal training, surgery and electrophysiology. We believe that the text in our current Discussion (line 465-468) accurately characterizes the situation:

“Our experimental design precludes an analysis of whether the reproducibility we observed was driven by person-to-person standardization or lab-to-lab standardization. Most likely, both factors contributed: all lab personnel received standardized instructions for how to implant head bars and train animals, which likely reduced personnel-driven differences.”

Quantifying the level of experience of each experimenter is an appealing idea and we share the reviewer’s curiosity about its impact on data quality. Unfortunately, quantifying experience is tricky. For instance, years of conducting surgeries is not an unambiguously determinable number. Would we count an experimenter who did surgery every day for a year as having the same experience as an experimenter who did surgery once/month for a year? Would we count a surgeon with expertise in other areas (e.g., windows for imaging) in the same way as surgeons with expertise in ephys-specific surgeries? Because of the ambiguities, we leave this analysis to be the subject of future work; this is now stated in the Discussion (line 476).

(3) Figure 3b and c: Are these plots before or after the probe depth has been adjusted based on physiological features such as the LFP power? In other words, is the IBL electrophysiological alignment toolbox used here and is the reliability of location before using physiological criteria or after? Beyond clarification, showing both before and after would help the readers to understand how much the additional alignment based on electrophysiological features adjusts probe location. It would also be informative if they sorted these penetrations by which penetrations were closest to the planned trajectory after histological verification.

The plots in Figure 3b and 3c reflect data after the probe depth has been adjusted based on electrophysiological features. This adjustment incorporates criteria such as LFP power and spiking activity to refine the trajectory and ensure precise alignment with anatomical landmarks. The trajectories have also been reviewed and confirmed by two independent reviewers. We have clarified this in line 180 and in the caption of Figure 3.

To address this concern, we have added a new panel c in Figure 3 supplementary 1 (also shown below) that shows the LFP features along the probes prior to using the IBL alignment toolbox. We hope the reviewer agrees that a comparison of panels (a) and (c) below make clear the improvement afforded by our alignment tools.

In Figure 3 and Figure 3 supplementary 1, as suggested, we have also now sorted the probes by those that were closest to the planned trajectory. This way of visualizing the data makes it clear that as the distance from the planned trajectory increases, the power spectral density in the hippocampal regions becomes less pronounced and the number of probes that have a large portion of the channels localized to VISa/am, LP and PO decreases. We have added text to the caption to describe this. We thank the reviewer for this suggestion and agree that it will help readers to understand how much the additional alignment (based on electrophysiological features) adjusts probe location.

(4) In Figures 4 and 6: If the authors use a 0.05 threshold (alpha) and a cell simply has to be significant on 1/6 tests to be considered task modulated, that means that they have a false positive rate of ~30% (0.05*6=0.3). We ran a simple simulation looking for significant units (from random null distribution) from these criteria which shows that out of 100.000 units, 26500 units would come out significant (false error rate: 26.5%). That is very high (and unlikely to be accepted in most papers), and therefore not surprising that the fraction of task-modulated units across labs is highly variable. This high false error rate may also have implications for the investigation of the spatial position of task-modulated units (as effects of the spatial position may drown in falsely labelled 'task-modulated' cells).

Thank you for this concern. The different tests were kept separate, so we did not consider a neuron modulated if it was significant in only one out of six tests, but instead we asked whether a neuron was modulated according to test one, whether it was modulated according to test two, etc., and performed further analyses separately for each test. Thus, we are only vulnerable to the ‘typical’ false positive rate of 0.05 for any given test. We made this clearer in the text (lines 232-236) and hope that the 5% false positive rate seems more acceptable.

(5) The authors state from Figure 5b that the majority of cells could be well described by 2 PCs. The distribution of R2 across neurons is almost uniform, so depending on what R2 value one considers a 'good' description, that is the fraction of 'good' cells. Furthermore, movement onset has now been well-established to be affecting cells widely and in large fractions, so while this analysis may work for something with global influence - like movement - more sparsely encoded variables (as many are in the brain) may not be well approximated with this suggestion. The authors could expand this analysis into other epochs like activity around stimulus presentation, to better understand how this type of analysis reproduces across labs for features that have a less global influence.

We thank the reviewer for the suggestion and fully agree that the window used in our original analysis would tend to favor movement-driven neurons. To address this, we repeated the analysis, this time using a window centered around stimulus onset (from -0.5 s prior to stimulus onset until 0.1 s after stimulus onset). As the reviewer suspected, far fewer neurons were active in this window and consequently far fewer were modelled well by the first two PCs, as shown in Author response image 1b (below). Similar to our original analysis using the post-movement window, we found mixed results for the stimulus-centered window across labs. Interestingly, regional differences were weaker in this new analysis compared to the original analysis of the post-movement window. We have added a sentence to the results describing this. Because the results are similar to the post-movement window main figure, we would prefer to restrict the new analysis only to this point-by-point response, in the hopes of streamlining the paper.

Author response image 1.

PCA analysis applied to a stimulus-aligned window ([-0.5, 0.1] sec relative to stim onset). Figure conventions as in main text Fig 5. Results are comparable to the post-movement window analysis, however regional differences are weaker here, possibly because fewer cells were active in the pre-movement window. We added panel j here and in the main figure, showing cell-number-controlled results. I.e. for each test, the minimum neuron number of the compared classes was sampled from all classes (say labs in a region), this sampling was repeated 1000 times and p-values combined via Fisher’s method, overall resulting in much fewer significant differences across laboratories and, independently, regions.

(6) Additionally, in Figure 5i: could the finding that one can only distinguish labs when taking cells from all regions, simply be a result of a different number of cells recorded in each region for each lab? It makes more sense to focus on the lab/area pairing as the authors also do, but not to make their main conclusion from it. If the authors wish to do the comparison across regions, they will need to correct for the number of cells recorded in each region for each lab. In general, it was a struggle to fully understand the purpose of Figure 5. While population analysis and dimensionality reduction are commonplace, this seems to be a very unusual use of it.

We agree that controlling for varying cell numbers is a valuable addition to this analysis. We added panel j in Fig. 5 showing cell-number-controlled test results of panel i. I.e. for a given statistical comparison, we sample the lowest number of cells of compared classes from the others, do the test, and repeat this sampling 1000 times, before combining the p-values using Fisher’s method. This cell-number controlled version of the tests resulted in clearly fewer significant differences across distributions - seen similarly for the pre-movement window shown in j in Author response image 1. We hope this clarified our aim to illustrate that low-dimensional embedding of cells’ trial-averaged activity can show how regional differences compare with laboratory differences.

As a complementary statistical analysis to the shown KS tests, we fitted a linear-mixed-effects model (statsmodels.formula.api mixedlm), to the first and second PC for both activity windows (“Move”: [-0.5,1] first movement aligned; “Stim”: [-0.5,0.1] stimulus onset aligned), independently. Author response image 2 (in this rebuttal only) is broadly in line with the KS results, showing more regional than lab influences on the distributions of first PCs for the post-movement window.

Author response image 2:

Linear mixed effects model results for two PCs and two activity windows. For the post-movement window (“Move”), regional influences are significant (red color in plots) for all but one region while only one lab has a significant model coefficient for PC1. For PC2 more labs and three regions have significant coefficients. For the pre-movement window (“Stim”) one region for PC1 or PC2 has significant coefficients. The variance due to session id was smaller than all other effects (“eids Var”). “Intercept” shows the expected value of the response variable (PC1, PC2) before accounting for any fixed or random effects. All p-values were grouped as one hypothesis family and corrected for multiple comparisons via Benjamini-Hochberg.

(7) In the discussion the authors state: " Indeed this approach is a more effective and streamlined way of doing it, but it is questionable whether it 'exceeds' what is done in many labs.

Classically, scientists trace each probe manually with light microscopy and designate each area based on anatomical landmarks identified with nissl or dapi stains together with gross landmarks. When not automated with 2-PI serial tomography and anatomically aligned to a standard atlas, this is a less effective process, but it is not clear that it is less precise, especially in studies before neuropixels where active electrodes were located in a much smaller area. While more effective, transforming into a common atlas does make additional assumptions about warping the brain into the standard atlas - especially in cases where the brain has been damaged/lesioned. Readers can appreciate the effectiveness and streamlining provided by these new tools without the need to invalidate previous approaches.

We thank the reviewer for highlighting the effectiveness of manual tracing methods used traditionally. Our intention in the statement was not to invalidate the precision or value of these classical methods but rather to emphasize the scalability and streamlining offered by our pipeline. We have revised the language to more accurately reflect this (line 500-504):

“Our ability to detect targeting error benefited from an automated histological pipeline combined with alignment and tracing that required agreement between multiple users, an approach that greatly exceeds the histological analyses done by most individual labs. Our approach, which enables scalability and standardization across labs while minimizing subjective variability, revealed that much of the variance in targeting was due to the probe entry positions at the brain surface, which were randomly displaced across the dataset.”

(8) What about across-lab population-level representation of task variables, such as in the coding direction for stimulus or choice? Is the general decodability of task variables from the population comparable across labs?

Excellent question, thanks! We have added the new section “Decodability of task variables is consistent across labs, but varies by brain region” (line 423-448) and Figure 9 in the revised manuscript to address this question. In short, yes, the general decodability of task variables from the population is comparable across labs, providing additional reassurance of reproducibility.

Reviewer #2 (Public review):

Summary:

The authors sought to evaluate whether observations made in separate individual laboratories are reproducible when they use standardized procedures and quality control measures. This is a key question for the field. If ten systems neuroscience labs try very hard to do the exact same experiment and analyses, do they get the same core results? If the answer is no, this is very bad news for everyone else! Fortunately, they were able to reproduce most of their experimental findings across all labs. Despite attempting to target the same brain areas in each recording, variability in electrode targeting was a source of some differences between datasets.

Major Comments:

The paper had two principal goals:

(1) to assess reproducibility between labs on a carefully coordinated experiment

(2) distill the knowledge learned into a set of standards that can be applied across the field.

The manuscript made progress towards both of these goals but leaves room for improvement.

(1) The first goal of the study was to perform exactly the same experiment and analyses across 10 different labs and see if you got the same results. The rationale for doing this was to test how reproducible large-scale rodent systems neuroscience experiments really are. In this, the study did a great job showing that when a consortium of labs went to great lengths to do everything the same, even decoding algorithms could not discern laboratory identity was not clearly from looking at the raw data. However, the amount of coordination between the labs was so great that these findings are hard to generalize to the situation where similar (or conflicting!) results are generated by two labs working independently.

Importantly, the study found that electrode placement (and thus likely also errors inherent to the electrode placement reconstruction pipeline) was a key source of variability between datasets. To remedy this, they implemented a very sophisticated electrode reconstruction pipeline (involving two-photon tomography and multiple blinded data validators) in just one lab-and all brains were sliced and reconstructed in this one location. This is a fantastic approach for ensuring similar results within the IBL collaboration, but makes it unclear how much variance would have been observed if each lab had attempted to reconstruct their probe trajectories themselves using a mix of histology techniques from conventional brain slicing, to light sheet microscopy, to MRI imaging.

This approach also raises a few questions. The use of standard procedures, pipelines, etc. is a great goal, but most labs are trying to do something unique with their setup. Bigger picture, shouldn't highly "significant" biological findings akin to the discovery of place cells or grid cells, be so clear and robust that they can be identified with different recording modalities and analysis pipelines?

We agree, and hope that this work may help readers understand what effect sizes may be considered “clear and robust” from datasets like these. We certainly support the reviewer’s point that multiple approaches and modalities can help to confirm any biological findings, but we would contend that a clear understanding of the capabilities and limitations of each approach is valuable, and we hope that our paper helps to achieve this.

Related to this, how many labs outside of the IBL collaboration have implemented the IBL pipeline for their own purposes? In what aspects do these other labs find it challenging to reproduce the approaches presented in the paper? If labs were supposed to perform this same experiment, but without coordinating directly, how much more variance between labs would have been seen? Obviously investigating these topics is beyond the scope of this paper. The current manuscript is well-written and clear as is, and I think it is a valuable contribution to the field. However, some additional discussion of these issues would be helpful.

We thank the reviewer for raising this important issue. We know of at least 13 labs that have implemented the behavioral task software and hardware that we published in eLife in 2021, and we expect that over the next several years labs will also implement these analysis pipelines (note that it is considerably cheaper and faster to implement software pipelines than hardware). In particular, a major goal of the staff in the coming years is to continue and improve the support for pipeline deployment and use. However, our goal in this work, which we have aimed to state more clearly in the revised manuscript, was not so much to advocate that others adopt our pipeline, but instead to use our standardized approach as a means of assessing reproducibility under the best of circumstances (see lines 48-52): “A high level of reproducibility of results across laboratories when procedures are carefully matched is a prerequisite to reproducibility in the more common scenario in which two investigators approach the same high-level question with slightly different experimental protocols.”

Further, a number of our findings are relevant to other labs regardless of whether they implement our exact pipeline, a modified version of our pipeline, or something else entirely. For example, we found probe targeting to be a large source of variability. Our ability to detect targeting error benefited from an automated histological pipeline combined with alignment and tracing that required agreement between multiple users, but now that we have identified the offset, it can be easily accounted for by any lab. Specifically, probe angles must be carefully computed from the CCF, as the CCF and stereotaxic coordinate systems do not define the same coronal plane angle. Relatedly, we found that slight deviations in probe entry position can lead to samples from different populations of neurons. Although this took large cohort sizes to discover, knowledge of this discovery means that future experiments can plan for larger cohort sizes to allow for off-target trajectories, and can re-compute probe angle when the presence of blood vessels necessitates moving probes slightly. These points are now highlighted in the Discussion (lines 500-515).

Second, the proportion of responsive neurons (a quantity often used to determine that a particular area subserves a particular function), sometimes failed to reproduce across labs. For example, for movement-driven activity in PO, UCLA reported an average change of 0 spikes/s, while CCU reported a large and consistent change (Figure 4d, right most panel, compare orange vs. yellow traces). This argues that neuron-to-neuron variability means that comparisons across labs require large cohort sizes. A small number of outlier neurons in a session can heavily bias responses. We anticipate that this problem will be remedied as tools for large scale neural recordings become more widely used. Indeed, the use of 4-shank instead of single-shank Neuropixels (as we used here) would have greatly enhanced the number of PO neurons we measured in each session. We have added new text to Results explaining this (lines 264-268):

“We anticipate that the feasibility of even larger scale recordings will make lab-to-lab comparisons easier in future experiments; multi-shank probes could be especially beneficial for cortical recordings, which tend to be the most vulnerable to low cell counts since the cortex is thin and is the most superficial structure in the brain and thus the most vulnerable to damage. Analyses that characterize responses to multiple parameters are another possible solution (See Figure 7).”

(2) The second goal of the study was to present a set of data curation standards (RIGOR) that could be applied widely across the field. This is a great idea, but its implementation needs to be improved if adoption outside of the IBL is to be expected. Here are three issues:

(a) The GitHub repo for this project (https://github.com/int-brain-lab/paper-reproducible-ephys/) is nicely documented if the reader's goal is to reproduce the figures in the manuscript. Consequently, the code for producing the RIGOR statistics seems mostly designed for re-computing statistics on the existing IBL-formatted datasets. There doesn't appear to be any clear documentation about how to run it on arbitrary outputs from a spike sorter (i.e. the inputs to Phy).

We agree that clear documentation is key for others to adopt our standards. To address this, we have added a section at the end of the README of the repository that links to a jupyter notebook (https://github.com/int-brain-lab/paper-reproducible-ephys/blob/master/RIGOR_script.ipynb) that runs the RIGOR metrics on a user’s own spike sorted dataset. The notebook also contains a tutorial that walks through how to visually assess the quality of the raw and spike sorted data, and computes the noise level metrics on the raw data as well as the single cell metrics on the spike sorted data.

(b) Other sets of spike sorting metrics that are more easily computed for labs that are not using the IBL pipeline already exist (e.g. "quality_metrics" from the Allen Institute ecephys pipeline [https://github.com/AllenInstitute/ecephys_spike_sorting/blob/main/ecephys_spike_sorting/m odules/quality_metrics/README.md] and the similar module in the Spike Interface package [https://spikeinterface.readthedocs.io/en/latest/modules/qualitymetrics.html]). The manuscript does not compare these approaches to those proposed here, but some of the same statistics already exist (amplitude cutoff, median spike amplitude, refractory period violation).

There is a long history of researchers providing analysis algorithms and code for spike sorting quality metrics, and we agree that the Allen Institute’s ecephys code and the Spike Interface package are the current options most widely used (but see also, for example, Fabre et al. https://github.com/Julie-Fabre/bombcell). Our primary goal in the present work is not to advocate for a particular implementation of any quality metrics (or any spike sorting algorithm, for that matter), but instead to assess reproducibility of results, given one specific choice of spike sorting algorithm and quality metrics. That is why, in our comparison of yield across datasets (Fig 1F), we downloaded the raw data from those comparison datasets and re-ran them under our single fixed pipeline, to establish a fair standard of comparison. A full comparison of the analyses presented here under different choices of quality metrics and spike sorting algorithms would undoubtedly be interesting and useful for the field - however, we consider it to be beyond the scope of the present work. It is therefore an important assumption of our work that the result would not differ materially under a different choice of sorting algorithm and quality metrics. We have added text to the Discussion to clarify this limitation:

“Another significant limitation of the analysis presented here is that we have not been able to assess the extent to which other choices of quality metrics and inclusion criteria might have led to greater or lesser reproducibility.”

That said, we still intend for external users to be able to easily run our pipelines and quality metrics.

(c) Some of the RIGOR criteria are qualitative and must be visually assessed manually. Conceptually, these features make sense to include as metrics to examine, but would ideally be applied in a standardized way across the field. The manuscript doesn't appear to contain a detailed protocol for how to assess these features. A procedure for how to apply these criteria for curating non-IBL data (or for implementing an automated classifier) would be helpful.

We agree. To address this, we have provided a notebook that runs the RIGOR metrics on a user’s own dataset, and contains a tutorial on how to interpret the resulting plots and metrics (https://github.com/int-brain-lab/paper-reproducible-ephys/blob/master/RIGOR_script.ipynb).

Within this notebook there is a section focused on visually assessing the quality of both the raw data and the spike sorted data. The code in this section can be used to generate plots, such as raw data snippets or the raster map of the spiking activity, which are typically used to visually assess the quality of the data. In Figure 1 Supplement 2 we have provided examples of such plots that show different types of artifactual activity that should be inspected.

Other Comments:

(1) How did the authors select the metrics they would use to evaluate reproducibility? Was this selection made before doing the study?

Our metrics were selected on the basis of our experience and expertise with extracellular electrophysiology. For example: some of us previously published on epileptiform activity and its characteristics in some mice (Steinmetz et al. 2017), so we included detection of that type of artifact here; and, some of us previously published detailed investigations of instability in extracellular electrophysiological recordings and methods for correcting them (Steinmetz et al. 2021, Windolf et al. 2024), so we included assessment of that property here. These metrics therefore represent our best expert knowledge about the kinds of quality issues that can affect this type of dataset, but it is certainly possible that future investigators will discover and characterize other quality issues.

The selection of metrics was primarily performed before the study (we used these assessments internally before embarking on the extensive quantifications reported here), and in cases where we refined them further during the course of preparing this work, it was done without reference to statistical results on reproducibility but instead on the basis of manual inspection of data quality and metric performance.

(2) Was reproducibility within-lab dependent on experimenter identity?

We thank the reviewer for this question. We have addressed it in our response to R1 General comment 2, as follows:

We agree that understanding experimenter-to-experimenter variability would be very interesting and indeed we had hoped to do this analysis for some time. The problem is that typically, each lab employed one trainee to conduct all the data collection. This prevents us from comparing outcomes from two different experimenters in the same lab. There are exceptions to this, such as the Churchland lab in which 3 personnel (two postdocs and a technician) collected the data. However, even this fortuitous situation did not lend itself well to assessing experimenter-to-experimenter variation: the Churchland lab moved from Cold Spring Harbor to UCLA during the data collection period, which might have caused variability that is totally independent of experimenter (e.g., different animal facilities). Further, once at UCLA, the postdoc and technician worked closely together- alternating roles in animal training, surgery and electrophysiology. We believe that the text in our current Discussion (line 465-468) accurately characterizes the situation:

“Our experimental design precludes an analysis of whether the reproducibility we observed was driven by person-to-person standardization or lab-to-lab standardization. Most likely, both factors contributed: all lab personnel received standardized instructions for how to implant head bars and train animals, which likely reduced personnel-driven differences.”

Quantifying the level of experience of each experimenter is an appealing idea and we share the reviewer’s curiosity about its impact on data quality. Unfortunately, quantifying experience is tricky. For instance, years of conducting surgeries is not an unambiguously determinable number. Would we count an experimenter who did surgery every day for a year as having the same experience as an experimenter who did surgery once/month for a year? Would we count a surgeon with expertise in other areas (e.g., windows for imaging) in the same way as surgeons with expertise in ephys-specific surgeries? Because of the ambiguities, we leave this analysis to be the subject of future work; this is now stated in the Discussion (line 476).

(3) They note that UCLA and UW datasets tended to miss deeper brain region targets (lines 185-188) - they do not speculate why these labs show systematic differences. Were they not following standardized procedures?

Thank you for raising this point. All researchers across labs were indeed following standardised procedures. We note that our statistical analysis of probe targeting coordinates and angles did not reveal a significant effect of lab identity on targeting error, even though we noted the large number of mis-targeted recordings in UCLA and UW to help draw attention to the appropriate feature in the figure. Given that these differences were not statistically significant, we can see how it was misleading to call out these two labs specifically. While the overall probe placement surface error and angle error both show no such systematic difference, the magnitude of surface error showed a non-significant tendency to be higher for samples in UCLA & UW, which, compounded with the direction of probe angle error, caused these probe insertions to land in a final location outside LP & PO.

This shows how subtle differences in probe placement & angle accuracy can lead to compounded inaccuracies at the probe tip, especially when targeting deep brain regions, even when following standard procedures. We believe this is driven partly by the accuracy limit or resolution of the stereotaxic system, along with slight deviations in probe angle, occurring during the setup of the stereotaxic coordinate system during these recordings.

We have updated the relevant text in lines 187-190 as follows, to clarify:

“Several trajectories missed their targets in deeper brain regions (LP, PO), as indicated by gray blocks, despite the lack of significant lab-dependent effects in targeting as reported above. These off-target trajectories tended to have both a large displacement from the target insertion coordinates and a probe angle that unfavorably drew the insertions away from thalamic nuclei (Figure 2f).”

(4) The authors suggest that geometrical variance (difference between planned and final identified probe position acquired from reconstructed histology) in probe placement at the brain surface is driven by inaccuracies in defining the stereotaxic coordinate system, including discrepancies between skull landmarks and the underlying brain structures. In this case, the use of skull landmarks (e.g. bregma) to determine locations of brain structures might be unreliable and provide an error of ~360 microns. While it is known that there is indeed variance in the position between skull landmarks and brain areas in different animals, the quantification of this error is a useful value for the field.

We thank the reviewer for their thoughtful comment and are glad that they found the quantification of variance useful for the field.

(5) Why are the thalamic recording results particularly hard to reproduce? Does the anatomy of the thalamus simply make it more sensitive to small errors in probe positioning relative to the other recorded areas?

We thank the reviewer for raising this interesting question. We believe that they are referring to Figure 4: indeed when we analyzed the distribution of firing rate modulations, we saw some failures of reproducibility in area PO (bottom panel, Figure 4h). However, the thalamic nuclei were not, in other analyses, more vulnerable to failures in reproducibility. For example, in the top panel of Figure 4h, VisAM shows failures of reproducibility for modulation by the visual stimulus. In Fig. 5i, area CA1 showed a failure of reproducibility. We fear that the figure legend title in the previous version (which referred to the thalamus specifically) was misleading, and we have revised this. The new title is, “Neural activity is modulated during decision-making in five neural structures and is variable between laboratories.” This new text more accurately reflects that there were a number of small, idiosyncratic failures of reproducibility, but that these were not restricted to a specific structure. The new analysis requested by R1 (now in Figure 7) provides further reassurance of overall reproducibility, including in the thalamus (see Fig. 7a, right panels; lab identity could not be decoded from single neuron metrics, even in the thalamus).

Reviewer #1 (Recommendations for the authors):

(1) Figure font sizes and formatting are variable across panels and figures. Please streamline the presentation of results.

Thank you for your feedback. We have remade all figures with the same standardized font sizes and formatting.

(2) Please correct the noncontinuous color scales in Figures 3b and 3d.

Thank you for pointing this out, we fixed the color bar.

(3) In Figures 5d and g, the error bars are described as: 'Error bands are standard deviation across cells normalised by the square root of the number of sessions in the region'. How does one interpret this error? It seems to be related to the standard error of the mean (std/sqrt(n)) but instead of using the n from which the standard deviation is calculated (in this case across cells), the authors use the number of sessions as n. If they took the standard deviation across sessions this would be the sem across sessions, and interpretable (as sem*1.96 is the 95% parametric confidence interval of the mean). Please justify why these error bands are used here and how they can be interpreted - it also seems like it is the only time these types of error bands are used.

We agree and for clarity use standard error across cells now, as the error bars do not change dramatically either way.

(4) It is difficult to understand what is plotted in Figures 5e,h, please unpack this further and clarify.

Thank you for pointing this out. We have added additional explanation in the figure caption (See caption for Figure 5c) to explain the KS test.

(5) In lines 198-201 the authors state that they were worried that Bonferroni correction with 5 criteria would be too lenient, and therefore used 0.01 as alpha. I am unsure whether the authors mean that they are correcting for multiple comparisons across features or areas. Either way, 0.01 alpha is exactly what a Bonferroni corrected alpha would be when correcting for either 5 features or 5 areas: 0.05/5=0.01. Or do they mean they apply the Bonferroni correction to the new 0.01 alpha: i.e., 0.01/5=0.002? Please clarify.

Thank you, that was indeed written confusingly. We considered all tests and regions as whole, so 7 tests * 5 regions = 35 tests, which would result in a very strong Bonferroni correction. Indeed, if one considers the different tests individually, the correction we apply from 0.05 to 0.01 can be considered as correcting for the number of regions, which we now highlight better. We apply no further corrections of any kind to our alpha=0.01. We clarified this in the manuscript in all relevant places (lines 205-208, 246, 297-298, and 726-727).

(6) Did the authors take into account how many times a probe was used/how clean the probe was before each recording. Was this streamlined between labs? This can have an effect on yield and quality of recording.

We appreciate the reviewer highlighting the potential impact of probe use and cleanliness on recording quality and yield. While we did not track the number of times each probe was used, we ensured that all probes were cleaned thoroughly after each use using a standardized cleaning protocol (Section 16: Cleaning the electrode after data acquisition in Appendix 2: IBL protocol for electrophysiology recording using Neuropixels probe). We acknowledge that tracking the specific usage history of each probe could provide additional insights, but unfortunately we did not track this information for this project. In prior work the re-usability of probes has been quantified, showing insignificant degradation with use (e.g. Extended Data Fig 7d from Jun et al. 2017).

(7) Figure 3, Supplement1: DY_013 missed DG entirely? Was this included in the analysis?

Thank you for this question. We believe the reviewer is referring to the lack of a prominent high-amplitude LFP band in this mouse, and lack of high-quality sorted units in that region. Despite this, our histology did localize the recording trajectory to DG. This recording did pass our quality control criteria overall, as indicated by the green label, and was used in relevant analyses.

The lack of normal LFP features and neuron yield might reflect the range of biological variability (several other sessions also have relatively weak DG LFP and yield, though DY_013 is the weakest), or could reflect some damage to the tissue, for example as caused by local bleeding. Because we could not conclusively identify the source of this observation, we did not exclude it.

(8) Given that the authors argue for using the MTNN over GLMs, it would be useful to know exactly how much better the MTNN is at predicting activity in the held-out dataset (shown in Figure 7, Supplement 1). It looks like a very small increase in prediction performance between MTNN and GLMs, is it significantly different?

The average variance explained on the held-out dataset, as shown in Figure 8–Figure Supplement 1 Panel B, is 0.065 for the GLMs and 0.071 for the MTNN. As the reviewer correctly noted, this difference is not significant. However, one of the key advantages of the MTNN over GLMs lies in its flexibility to easily incorporate covariates, such as electrophysiological characteristics or session/lab IDs, directly into the analysis. This feature is particularly valuable for assessing effect sizes and understanding the contributions of various factors.

(9) In line 723: why is the threshold for mean firing rate for a unit to be included in the MTNN results so high (>5Hz), and how does it perform on units with lower firing rates?      

We thank the reviewer for pointing this out. The threshold for including units with a mean firing rate above 5 Hz was set because most units with firing rates below this threshold were silent in many trials, and reducing the number of units helped keep the MTNN training time reasonable. Based on this comment, we ran the MTNN experiments including all units with firing rates above 1 Hz, and the results remained consistent with our previous conclusions (Figure 8). Crucially, the leave-one-out analysis consistently showed that lab and session IDs had effect sizes close to zero, indicating that both within-lab and between-lab random effects are small and comparable.

Reviewer #2 (Recommendations for the authors):

(1) Most of the more major issues were already listed in the above comments. The strongest recommendation for additional work would be to improve the description and implementation of the RIGOR statistics such that non-IBL labs that might use Neuropixels probes but not use the entire IBL pipeline might be able to apply the RIGOR framework to their own data.

We thank the reviewer for highlighting the importance of making the RIGOR statistics more accessible to a broader audience. We agree that improving the description and implementation of the RIGOR framework is essential for facilitation of non-IBL labs using Neuropixels probes. To address this we created a jupyter notebook with step-by-step guidance that is not dependent on the IBL pipeline. This tool (https://github.com/int-brain-lab/paper-reproducible-ephys/blob/develop/RIGOR_script.ipynb) is publicly available through the repository, accompanied by example datasets and usage tutorials.

(2) Table 1: How are qualitative features like "drift" defined? Some quantitative statistics like "presence ratio" (the fraction of the dataset where spikes are present) already exist in packages like ecephys_spike_sorting. Who measured these qualitative features? What are the best practices for doing these qualitative analyses?

At the probe level, we compute the estimate of the relative motion of the electrodes to the brain tissue at multiple depths along the electrode. We overlay the drift estimation over a raster plot to detect sharp displacements as a function of time. Quantitatively, the drift is the cumulative absolute electrode motion estimated during spike sorting (µm). We clarified the corresponding text in Table 1.

The qualitative assessments were carried out by IBL staff and experimentalists. We have now provided code to run the RIGOR metrics along with an embedded tutorial, to complement the supplemental figures we have shown about qualitative metric interpretation.

(3) Table 1: What are the units for the LFP derivative?

We thank the reviewer for noting that the unit was missing. The unit (decibel per unit of space) is now in the table.

(4) Table 1: For "amplitude cutoff", the table says that "each neuron must pass a metric". What is the metric?

We have revised the table to include this information. This metric was designed to detect potential issues in amplitude distributions caused by thresholding during deconvolution, which could result in missed spikes. There are quantitative thresholds on the distribution of the low tail of the amplitude histogram relative to the high tail, and on the relative magnitude of the bins in the low tail. We now reference the methods text from the table, which includes a more extended description and gives the specific threshold numbers. Also, the metric and thresholds are more easily understood with graphical assistance; see the IBL Spike Sorting Whitepaper for this (Fig. 17 in that document and nearby text; https://doi.org/10.6084/m9.figshare.19705522.v4). This reference is now also cited in the text.

(5) Figure 2: In panel A, the brain images look corrupted.

Thanks; in the revised version we have changed the filetype to improve the quality of the panel image.

(6) Figure 7: In panel D, make R2 into R^2 (with a superscript)

Panel D y-axis label has been revised to include superscript (note that this figure is now Figure 8).

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Author response:

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

eLife assessment

This important study presents a novel pipeline for the large-scale genomic prediction of members of the non-ribosomal peptide group of pyoverdines based on a dataset from nearly 2000 Pseudomonas genomes. The advance presented in this study is largely based on solid evidence, although some main claims are only incompletely supported. This study on bacterial siderophores has broad theoretical and practical implications beyond a singular subfield.

Thank you for the supportive and encouraging words. We appreciate the editor’s and reviewers’ careful and professional assessment of this manuscript. The reviewers’ scrutiny has helped us to improve the presentation and discussion of our work. We have now carefully revised the manuscript following their instructive suggestions and comments. Please find below our detailed responses (marked in blue) to each of the comments.

Public Reviews:

Reviewer #1 (Public Review):

The manuscript introduces a bioinformatic pipeline designed to enhance the structure prediction of pyoverdines, revealing an extensive and previously overlooked diversity in siderophores and receptors. Utilizing a combination of feature sequence and phylogenetic approaches, the method aims to address the challenging task of predicting structures based on dispersed gene clusters, particularly relevant for pyoverdines.

Predicting structures based on gene clusters is still challenging, especially pyoverdines as the gene clusters are often spread to different locations in the genome. An improved method would indeed be highly useful, and the diversity of pyoverdine gene clusters and receptors identified is impressive.

However, so far the method basically aligns the structural genes and domains involved in pyoverdine biosynthesis and then predicts A domain specificity to predict the encoded compounds. Both methods are not particularly new as they are included in other tools such as PRISM (10.1093/nar/gkx320) or Sandpuma (https://doi.org/10.1093/bioinformatics/btx400) among others. The study claims superiority in A domain prediction compared to existing tools, yet the support is currently limited, relying on a comparison solely with AntiSMASH. A more extensive and systematic comparison with other tools is needed.  

Thanks for pointing this out. In the revised manuscript, we have included a comprehensive comparative analysis, in which we compared our pipeline to six different commonly used methods, including NP.searcher, PRISM4, AdenPredictor, SeMPI2, SANDPUMA, antiSMASH5 (see Supplementary_table 6 for details, and lines 281-286). These approaches either consist of a single specific algorithm or integrate several methods. Our approach performs best (see table below), demonstrating a clear improvement over previous tool. The improvements are due to several methodological differences inherent to our approach. Additionally, while exploring existing prediction tools, we found that some had not been maintained for years. For instance, we were unable to access NRPSsp (www.nrpssp.com) and NRPSpredictor2 (http://nrps.informatik.uni-tuebingen.de/). Below, we briefly explain these differences, particularly in relation to PRISM and SANDPUMA, as highlighted by the reviewer. 

Author response table 1.

PRISM annotates biosynthetic gene clusters (BGC) and reconstructs the linear structures of NRPS synthetases, with this function depending on proper annotations of open reading frames. This pipeline can have difficulties in assembling the linear structure into a final product. In our approach, we found that the annotations of NRPS gene are frequently truncated because of sequencing errors and annotation issues. Our method fixes this problem through rescanning all possible reading frames of the BGC to rebuild complete pyoverdine synthetase genes. 

Sandpum and our approach are based on similar ideas (using the prediCAT algorithm) to predict A domain substrates, namely by using the closest reference A domain annotated. However, our method uses a self-adaptive feature extraction step to reduce the co-founding influence of phylogeny. This small adjustment significantly improves the performance of our approach and even works well for small training sets (101 experimentally validated A domains with our approach as opposed to 494 A domains used by Sandpuma from MIBiG).

Additionally, in contradiction to the authors' claims, the method's applicability seems constrained to well-known and widely distributed gene clusters. The absence of predictions for new amino acids raises concerns about its generalizability to NRPS beyond the studied cases.

We thank the reviewers for this comment. We acknowledge that our method cannot directly predict new amino acids. Nevertheless, for several reasons we believe that our approach is not constrained and can be widely applied in the future.

First, our method can identify A domains that select new unknown amino acid substrates. In fact, three of the four unresolved cases in our experimental verification analysis (Fig. 3d) represent new amino acids. Obviously, experimental verification is required to characterize the unknown substrate. Once verified, the new A domains and their substrates can expand the reference dataset, allowing targeted improvement of our phylogeny-focused prediction technique. We now discuss this aspect in lines 634-645.

Second, despite that the overall substrate diversity in NRPS is high across the microbial kingdom, our analysis suggests that the number of amino acids used for a specific group of secondary metabolites quickly reaches a saturation point. The discovery rate of new amino acids was 1.7% for our experimental Pseudomonas data set (Fig. 3d). The discovery rate of new amino acids was even 0.0 % for the Burkholderiales data set. This suggests that as the database expands, the discovery rate of novel amino acid substrates is expected to drop rapidly.

Third, we acknowledge that the inability to predict the substrates of unknown domains is a common limitation among all knowledge-guided learning algorithms, including ours. However, we have made significant improvements in prediction accuracy. As the database grows, we expect the rate of unknown substrates to decrease, and the prediction accuracy to increase.

The manuscript lacks clarity on how the alignment of structural genes operates when dealing with multiple NRPS gene clusters on different genome contigs. How would the alignment of each BGC work?

We thank the reviewers for this comment. The pyoverdine molecules consist of a conserved fluorescent chromophore (Flu) and a peptide chain (Pep), both synthesized by NRPS enzymes. In most instances (over 90%), Flu and Pep are produced by two separate biosynthetic gene clusters (BGCs). In these cases, we merge the two BGCs by positioning Flu at the head and Pep at the tail. For the remaining less than 10%, there are two scenarios: 1. Flu and Pep are located on the same BGC, which eliminates any issues with BGC alignment. 2. In very rare cases, Flu and Pep are synthesized by three BGCs. Here, Flu is still synthesized by one BGC at the head, while Pep is produced by two BGCs. We put the BGC containing the Thioesterase (TE) domain as the tail and the BGC not containing the TE domain in the middle.

(see lines 165-169).

Another critical concern is that a main challenge in NRPS structure prediction is not the backbone prediction but rather the prediction of tailoring reactions, which is not addressed in the manuscript at all, and this limitation extensively restricts the applicability of the method.

While we thank the reviewer for this comment, we only partly agree with it. Peptide backbone predictions are still a significant challenge. This challenge is clearly visible in our new analysis comparing prediction accuracies of different pipelines, such as antiSMASH5, PRISM4, AdenPredictor, SeMPI2, NP.searcher, Sandpuma. Unresolved and wrong substrate predictions are still common, highlighting the importance of our contribution in developing a new approach with improved high accuracy. 

However, we agree with the reviewer that our current algorithm does not predict tailoring reactions (now discussed on lines 680-685). Although tailoring reactions are important for predicting the final NRPS product structure, none of the other existing pipelines address this issue either, and it remains a challenge for future work. For our study, it is important to note that the specificity of pyoverdines is primarily determined by the backbone composition, whereas tailoring reactions seem to play a minor role.

The manuscript presents a potentially highly useful bioinformatic pipeline for pyoverdine structure prediction, showcasing a commendable exploration of siderophore diversity. However, some of the claims made remain unsubstantiated. Overall, while the study holds promise, further validation and refinement are required to fulfill its potential impact on the field of bioinformatic structure prediction.

Thank you for the supportive and encouraging words. We deeply appreciate your constructive comments and suggestions. 

Reviewer #2 (Public Review):

Pyoverdines, siderophores produced by many Pseudomonads, are one of the most diverse groups of specialized metabolites and are frequently used as model systems. Thousands of Pseudomonas genomes are available, but large-scale analyses of pyoverdines are hampered by the biosynthetic gene clusters (BGCs) being spread across multiple genomic loci and existing tools' inability to accurately predict amino acid substrates of the biosynthetic adenylation (A) domains. The authors present a bioinformatics pipeline that identifies pyoverdine BGCs and predicts the A domain substrates with high accuracy. They tackled a second challenging problem by developing an algorithm to differentiate between outer membrane receptor selectivity for pyoverdines versus other siderophores and substrates. The authors applied their dataset to thousands of Pseudomonas strains, producing the first comprehensive overview of pyoverdines and their receptors and predicting many new structural variants.

The A domain substrate prediction is impressive, including the correction of entries in the MIBiG database. Their high accuracy came from a relatively small training dataset of A domains from 13 pyoverdine BGCs. The authors acknowledge that this small dataset does not include all substrates, and correctly point out that new sequence/structure pairs can be added to the training set to refine the prediction algorithm. 

The authors could have been more comprehensive in finding their training set data. For instance, the authors claim that histidine "had not been previously documented in pyoverdines", but the sequenced strain P. entomophila L48, incorporates His (10.1007/s10534-009-9247-y). 

Thank you for highlighting this issue. We agree that stating histidine has not been reported before in pyoverdine was incorrect. We have reviewed the full text and made the necessary corrections.

The primary reason for excluding the sequenced strains P. syringae 1448a (10.1186/14712180-11-218) and P. entomophila L48 (10.1007/s10534-009-9247-y) from the training set is that the pyoverdine structures of these strains were not determined solely through experimental methods. In these works, the pyoverdine structures were predicted based on the synthetic gene sequence using bioinformatical analysis, followed by structural analysis experiments based on this predicted structure. We found that pre-prediction probably has introduced biases into downstream analyses. Specifically, in the case of Pseudomonas entomophila L48, we discovered inaccuracies in the annotation of certain domains (see figures below). For example, the third A domain of the peptide chain in P. entomophila L48 pyoverdine was initially annotated with Dab specificity. However, upon closer examination, it appears to differ significantly from other Dab references (top) or Dab from our experimentally validated (right) domains (left panel in the figure below). By analyzing the interface (I) domain (10.1073/pnas.1903161116) in its predicted site, we suggested that it should actually recognize OHHis. The OHAsp domain of P. entomophila L48 reported in the paper is actually close in sequence similarity to the OHAsp domain (left panel in the figure below), while the Ala domain reported is more similar to the Ser domain (right panel in the figure below). For these reasons, we did not include this supervised pyoverdine structure analysis strain in the training set data.

Author response image 1.

The workflow cannot differentiate between different variants of Asp and OHOrn, and it's not clear if this is a limitation of the workflow, the training data, or both. 

Thanks for pointing this out. It is generally challenging to differentiate between variants of the same amino acid (for all the algorithms existing to date). In this sense, it is a limitation of our but also of all other workflows. Nonetheless, we wish to stress that we observed feature sequence divergence (using the A motif4-5 region), which helped us to separate some (but not all) of the Asp and Orn variants. For example, separations between Asp-variants are distinct (left panel in the figure below). To be on the conservative side, we only differentiated between OHAsp and Asp for our predictions, but also differentiation between DOHAsp and OHAsp would be possible. In the case of Orn-variants, there was a clear separation between Orn and the OHOrn variants (right panel). In contrast, it was difficult to differentiate between the subgroups of OHOrn variants. We believe that no A domain prediction tool will be able to solve this issue. Instead, it would be important to include information on substrate-modifying enzymes in future approaches.

Author response image 2.

The prediction workflow holds up well in Burkholderiales A domains, however, they fail to mention in the main text that they achieved these numbers by adding more A domains to their training set.

We thank the reviewers for this comment. We apologize for not having mentioned the training data set in the main text, while we described it in detail in the methods section (lines 714-732). We now provided more details on the analysis procedure in the main text (lines 307313). Important to note is that we did not add more A domains to the training data set but built up a new independent data set for Burkholderiales. The aim was to mirror the analysis we performed for pyoverdines with a completely new data set, featuring 124 A domains for training and 178 A domains as test set.

To validate their predictions, they elucidated structures of several new pyoverdines, and their predictions performed well. However, the authors did not include their MS/MS data, making it impossible to validate their structures. In general, the biggest limitation of the submitted manuscript is the near-empty methods section, which does not include any experimental details for the 20 strains or details of the annotation pipeline (such as "Phydist" and "Syndist"). The source code also does not contain the requisite information to replicate the results or re-use the pipeline, such as the antiSMASH version and required flags. That said, skimming through the source code and data (kindly provided upon request) suggests that the workflow itself is sound and a clear improvement over existing tools for pyoverdine BGC annotation.

Thank you for highlighting these issues. We agree that the methods section is short. This is because the entire paper is a step-by-step methodological introduction to our pipeline. We have now carefully revised the main text to add the information requested by the reviewer. Moreover, we have included a supplementary file with the MS/MS data of the experimentally analyzed pyoverdine structures. Finally, we further include a link to a one-click online notebook that can be used to replicate the annotation and substrate prediction results See: https://drive.google.com/drive/folders/1JsfyPUGDTFo8BDDZk8JLSvKry8emzMhr?usp=drive_ link , following a more detail explanation on code.

Predicting outer membrane receptor specificity is likewise a challenging problem and the authors have made a promising achievement by finding specific gene regions that differentiate the pyoverdine receptor FpvA from FpvB and other receptor families. Their predictions were not tested experimentally, but the finding that only predicted FpvA receptors were proximate to the biosynthesis genes lends credence to the predictive power of the workflow. The authors find predicted pyoverdine receptors across an impressive 468 genera, an exciting finding for expanding the role of pyoverdines as public goods beyond Pseudomonas. However, whether or not these receptors can recognize pyoverdines (and if so, which structures!) remains to be investigated.

Thank you for the supportive and encouraging words. The bioinformatic analysis and experimental testing of pyoverdine-receptor matching is complicated and it is not part of this paper. We treated it in a separate manuscript in which we developed an experimentally verified co-evolution algorithm that matches pyoverdines to receptors. With this algorithm, we can identify self-receptors (i.e. receptors used to take up the self-produced pyoverdine), and therefore establish pyoverdine sharing and interaction networks across strains in communities.

Please see DOI:10.1101/2023.11.05.565711 for details.

In all, the authors have assembled a rich dataset that will enable large-scale comparative genomic analyses. This dataset could be used by a variety of researchers, including those studying natural product evolution, public good eco/evo dynamics, and NRPS engineering.

Thank you for the supportive and encouraging words. We are grateful for the reviewers’ instructive suggestions and comments.

Reviewer #3 (Public Review):

Summary:

Secondary metabolites are produced by numerous microorganisms and have important ecological functions. A major problem is that neither the function of a secondary metabolite enzyme nor the resulting metabolite can be precisely predicted from gene sequence data.

In the current paper, the authors addressed this highly relevant question.

The authors developed a bioinformatic pipeline to reconstruct the complete secondary metabolism pathway of pyoverdines, a class of iron-scavenging siderophores produced by Pseudomonas spp. These secondary metabolites are biosynthesized by a series of nonribosomal peptide synthetases and require a specific receptor (FpvA) for uptake. The authors combined knowledge-guided learning with phylogeny-based methods to predict with high accuracy encoding NRPSs, substrate specificity of A domains, pyoverdine derivatives, and receptors. After validation, the authors tested their pipeline with sequence data from 1664 phylogenetically distinct Pseudomonas strains and were able to determine 18,292 enzymatic A domains involved in pyoverdine synthesis, reliably predicted 97.8% of their substrates, identified 188 different pyoverdine molecule structures and 4547 FpvA receptor variants belonging to 94 distinct groups. All the results and predictions were clearly superior to predictions that are based on antiSMASH. Novel pyoverdine structures were elucidated experimentally by UHPLC-HR-MS/MS.

To assess the extendibility of the pipeline, the authors chose Burkholderiales as a test case which led to the results that the pipeline consistently maintains high prediction accuracy within Burkholderiales of 83% which was higher than for antiSMASH (67%).

Together, the authors concluded that supervised learning based on a few known compounds produced by species from the same genus probably outperforms generalized prediction algorithms trained on many products from a diverse set of microbes for NRPS substrate predictions. As a result, they also show that both pyoverdine and receptor diversity have been vastly underestimated.

Strengths:

The authors developed a very useful bioinformatic pipeline with high accuracy for secondary metabolites, at least for pyoverdines. The pipelines have several advantages compared to existing pipelines like the extensively used antiSMASH program, e.g. it can be applied to draft genomes, shows reduced erroneous gene predictions, etc. The accuracy was impressively demonstrated by the discovery of novel pyoverdines whose structures were experimentally substantiated by UHPLC-HR-MS/MS.

The manuscript is very well written, and the data and the description of the generation of pipelines are easy to follow.

Weaknesses:

The only major comment I have is the uncertainty of whether the pipeline can be applied to more complex non-ribosomal peptides. In the current study, the authors only applied their pipeline to a very narrow field, i.e., pyoverdines of Pseudomonas and Burkholderia strains.

Thanks for your positive and encouraging comment. Regarding your only major comment, we think that the design concept of our pipeline has the potential to be applied to more complex non-ribosomal peptides. Currently, our method is tailored to accurately predict the structural composition of the Pseudomonas siderophore pyoverdine (see also response 3). A key point emphasized in our article is the importance of considering phylogeny in developing substrate prediction algorithms for A domains. Currently, the main challenge in advancing these algorithms is the limited availability of data on A domains and their corresponding substrates. However, with the future accumulation of more reference data, we are confident that the design principles of our method will enable precise predictions of the structural compositions of all products synthesized by non-ribosomal peptide synthetases (see our discussions in lines 634-

645). 

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I believe that the manuscript would benefit from focusing solely on the task of improving pyoverdine predictions. This aspect alone is significant, and robustly supporting this claim would strengthen the manuscript. The diversity analysis provided is valuable and would undoubtedly benefit the scientific community. However, additional systematic comparisons with other methods are necessary. Furthermore, clarification of certain terms, such as 'featurebased' (e.g., whether it refers to NRPS domains or CDS), would enhance clarity.

Thank you for the supportive and encouraging words. We followed the reviewer’s suggestion and now provide the requested method comparison, see also response 2 for details. Furthermore, we have carefully checked the main text to clarify terms whenever needed. Specifically, we now define the terms “feature sequence” and “feature sequence distance” in lines 227-229.  

Additionally, several minor points could be improved upon:

In line 85, clarification is needed on how pyoverdine genes were identified.

Thank you for your thorough review. In the introduction section, we provided a brief overview of our work, while the detailed methodology is outlined in the results section on lines 160-174.

In line 382, it would be helpful to know the source of the sequences.

We agree and have now carefully revised the manuscript following your suggestions (lines 403-405).

Line 392 could be explained more clearly. Does it mean that the authors used an hmm search to search pHMMs against each reference sequence?

Thanks for your comment. Yes, we used an hmm search to search pHMMs against each reference sequence. We have now revised the manuscript to improve explanations (lines 413-418).

Reviewer #2 (Recommendations For The Authors):

The authors state they "elucidated the chemical structure of the 20 pyoverdines using culturebased methods combined with UHPLC-HR-MS/MS", so I was alarmed to see that KR and LB already published several of those structures in the cited paper. I hope that this "double dipping" will be fixed in a revision process.

Thank you for pointing this out. We agree that we have not explained clearly enough what steps were conducted in this study and which data were used from a previous paper (https://doi.org/10.1007/s00216-022-03907-w). The genomes of the 20 strains used for the verification analysis (Fig. 3d) were sequenced as part of this study (access code now provided). 14 out of the 20 pyoverdine structures were elucidated with UHPLC-HR-MS/MS in this study. For 6 out of the 20 pyoverdines, we had structural information already at hand from the previous paper. We have now clarified these details in our manuscript (lines 276-280). 

Thank you for providing the source code and data, and I hope that the final non-redundant dataset will be uploaded to Zenodo or another repository. Please deposit the 20 newlysequenced genomes to GenBank or another public repository. Please also show the UHPLC-

HR-MS/MS data, preferably in the form of raw data uploaded to GNPS.

We have followed the reviewer’s advice and deposited our data:

- The sequences of the 20 newly sequenced strains are available on ENA accession PRJEB76792.

- The MS/MS plots of the 14 newly analyzed pyoverdines are shown in the Supplementary Materials.

- We provide a one-click online notebook to allow readers to replicate the pyoverdine cluster annotation and substrate prediction of the 20 experimentally analyzed strains.

I suggest adding "at least" or a similar qualifier when the 73 variants are mentioned unless the literature search was truly exhaustive. What were the criteria for inclusion of the 13 strains in Table S2? For instance, sequenced strains P. syringae 1448a (10.1186/1471-2180-11-218) and P. entomophila L48 (10.1007/s10534-009-9247-y) were not included.

Thank you for your comment. We have now carefully revised the manuscript following your suggestions (lines 291-295). Regarding the criteria for including the 13 strains in Table S2, we aimed to select strains with the high credibility for inclusion in the training set data. The primary reason for excluding the two strains from the training set is that their siderophore structures were analyzed through supervised experiments. We wanted to avoid any form of biases that bioinformatic pre-predictions could introduce to downstream analyses (see Response 13 for details).

OHAsp in pyoverdines has been reported to arise from hydroxylation of Asp after it's already been activated by the A domain (10.1073/pnas.1903161116). Was there a clear difference between A domains that lead to Asp and OHAsp? Conversely, acetylation and formylation of OHOrn occur before adenylation. Can your workflow be used to differentiate cOHOrn, fOHOrn, and AcOHOrn, which are currently difficult to predict through genome mining?

Thank you for these considerations. We treated these aspects in our response 8.  

Throughout, define non-proteinogenic AA substrate abbreviations (ex: Rsc, Dab).

Revised as per suggestion (lines 329-333).

Additional line comments:

189: Mention PhyloPhlAn in the main text.

Revised as per suggestion (lines 189).

191: Define these filtering/selection criteria.

Thanks for your comment, we have added the criteria in the main text (line 196 and line 198). 

309, 620: An A domain presumably loading histidine is present in sequenced strain P. entomophila L48 (10.1007/s10534-009-9247-y). Please also clarify that Val has previously been seen in a pyoverdine (it is in Table S1) albeit not sequenced.

We have clarified these aspects as per suggestion (lines 314-315 and line 630).

310: The pipeline can "highlight" new substrates, but not identify them.

Revised as per suggestion (line 295).

354: Please clarify "13 amino acid substrates form the core of all the 188 pyoverdine structures", considering that 279 A domain substrates couldn't be predicted.

Thanks for your comments. We have now clarified “our analysis found that 13 amino acids form the main structural substrates of all the 188 pyoverdine structures.” (lines

360-363)

630: "discovered" implies that there is experimental evidence. I suggest something like "here we predicted 151 putatively new variants".

Revised as per suggestion (line 648).

Reviewer #3 (Recommendations For The Authors):

Weakness:

The only major comment I have is the uncertainty of whether the pipeline can be applied to more complex non-ribosomal peptides. In the current study, the authors only applied their pipeline to a very narrow field, i.e., pyoverdines of Pseudomonas and Burkholderia strains

Thanks for your comment. Please see our Responses 3+13 above, where we treat this concern in detail. Moreover, we discussed the possibility of extension to other groups of secondary metabolites in our discussion. We believe that we deliver a balanced view on the applicability of our approach and the next steps to be taken.  

Please comment on this aspect.

Minor:

(1)  When you speak about "synthesis" it is rather biosynthesis. Synthesis is chemical synthesis.

Please replace all instances of the word synthesis with biosynthesis.

Revised as per suggestion.

(2)  Line 188: synthetase is rather synthetases

Revised as per suggestion (line 191).

Author response:

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

Reviewer #1 (Public review):

Summary:

In this manuscript, Herrmannova et al explore changes in translation upon individual depletion of three subunits of the eIF3 complex (d, e and h) in mammalian cells. The authors provide a detailed analysis of regulated transcripts, followed by validation by RT-qPCR and/or Western blot of targets of interest, as well as GO and KKEG pathway analysis. The authors confirm prior observations that eIF3, despite being a general translation initiation factor, functions in mRNA-specific regulation, and that eIF3 is important for translation re-initiation. They show that global effects of eIF3e and eIF3d depletion on translation and cell growth are concordant. Their results support and extend previous reports suggesting that both factors control translation of 5'TOP mRNAs. Interestingly, they identify MAPK pathway components as a group of targets coordinately regulated by eIF3 d/e. The authors also discuss discrepancies with other reports analyzing eIF3e function.

Strengths:

Altogether, a solid analysis of eIF3 d/e/h-mediated translation regulation of specific transcripts. The data will be useful for scientists working in the Translation field.

Weaknesses:

The authors could have explored in more detail some of their novel observations, as well as their impact on cell behavior.

The manuscript has improved with the new corrections. I appreciate the authors' attention to the minor comments, which have been fully solved. The authors have not, however, provided additional experimental evidence that uORF-mediated translation of Raf-1 mRNA depends on an intact eIF3 complex, nor have they addressed the consequences of such regulation for cell physiology. While I understand that this is a subject of follow-up research, the authors could have at least included their explanations/ speculations regarding major comments 2-4, which in my opinion could have been useful for the reader.

Our explanations/speculations regarding major comments 2 and 3 were included in the Discussion. We apologize for this misunderstanding as we thought that we were supposed to explain our ideas only in the responses. We did not discuss the comment 4, however, as we are really not sure what is the true effect and did not want to go into wild speculations in our manuscript. We thank this reviewer for his insightful comments and understanding.

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

Reviewer #1 (Recommendations For The Authors):

Major comments:

(1) The authors report the potential translational regulation of Raf kinase by re-initiation. It would be interesting to show that Raf is indeed regulated by uORF-mediated translation, and that this is dependent on an intact eIF3 complex. Analyzing the potential consequences of Raf1 regulation for cancer cell proliferation or apoptosis would be a plus.

We agree that this is an interesting and likely possibility. In fact, another clue that translation of Raf1 is regulated by uORFs comes from Bohlen et al. 2023 (PMID: 36869665) where they showed that RAF1 translation is dependent on PRRC2 proteins (that promote leaky scanning through these uORFs). We noted in the discussion that our results from eIF3d/e/hKD and the PRRC2A/B/CKD partly overlap. It is a subject of our follow-up research to investigate whether eIF3 and PRRC2 co-operate together to regulate translation of this important mRNA. 

(2) The authors show that eIF3 d/e -but not 3h- has an effect on cell proliferation. First, this indicates that proliferation does not fully correlate with eIF3 integrity. Depletion of eIF3d does not affect the integrity of eIF3, yet the effects on proliferation are similar to those of eIF3e. What is the possibility that changes in proliferation reflect functions of eIF3d outside the eIF3 complex? What could be the real consequences of disturbing eIF3 integrity for the mammalian cell? Please, discuss.

Yes, proliferation does not fully correlate with eIF3 integrity. Downregulation of eIF3 subunits that lead to disintegration of eIF3 YLC core (a, b, c, g, i) have more detrimental effect on growth and translation than downregulation of the peripheral subunits (e, k, l, f, h, m). Our previous studies (Wagner et al. 2016, PMID: 27924037 and Herrmannová et al. 2020, PMID: 31863585) indicate that the YLC core of eIF3 can partially support translation even without its peripheral subunits. In this respect eIF3d (as a peripheral subunit) is an amazing exception, suggesting it may have some specialized function(s). Whether this function resides outside of the eIF3 complex or not we do not know, but do not think so. Mainly because in the absence of eIF3e – its interaction partner, eIF3d gets rapidly degraded. Therefore, it is not very likely that eIF3d exists alone outside of eIF3 complex with moonlighting functions elsewhere. We think that eIF3d, as a head-interacting subunit close to an important head ribosomal protein RACK1 (a landing pad for regulatory proteins), is a target of signaling pathways, which may make it important for translation of specific mRNAs. In support is these thoughts, eIF3d (in the context of entire eIF3) together with DAP5 were shown to promote translation by an alternate capdependent (eIF4F-independent) mechanism (Lee et al. 2016, PMID: 27462815; de la Parra et al. 2018, PMID:30076308). In addition, the eIF3d function (also in the context of entire eIF3) was proved to be regulated by stress-triggered phosphorylation (Lamper et al. 2020, PMID: 33184215). 

(3) Figure 6D: Surprisingly, reduced levels of ERK1/2 upon eIF3d/e-KD are compensated by increased phosphorylation of ERK1/2 and net activation of c-Jun. Please comment on the functional consequences of buffering mechanisms that the cell deploys in order to counteract compromised eIF3 function. Why would the cell activate precisely the MAPK pathway to compensate for a compromised eIF3 function?

This we do not know. We can only speculate that when translation is compromised, cells try to counteract it in two ways: 1) they produce more ribosomes to increase translational rates and 2) activate MAPK signaling to send pro-growth signals, which can in the end further boost ribosome biogenesis.

(4) Regarding DAP-sensitive transcripts, can the authors discuss in more detail the role of eIF3d in alternative cap-dependent translation versus re-initiation? Are these transcripts being translated by a canonical cap- and uORF-dependent mechanism or by an alternative capdependent mechanism?

This is indeed not an easy question. On one hand, it was shown that DAP5 facilitates translation re-initiation after uORF translation in a canonical cap-dependent manner. This mechanism is essential for translation of the main coding sequence (CDS) in mRNAs with structured 5' leaders and multiple uORFs. (Weber et al. 2022, PMID: 36473845; David et al., 2022, PMID: 35961752). On the other hand, DAP5 was proposed to promote alternative, eIF4F-independent but cap-dependent translation, as it can substitute the function of the eIF4F complex in cooperation with eIF3d (de la Parra et al., 2018, PMID: 30076308; Volta et al., 2021 34848685). Overall, these observations paint a very complex picture for us to propose a clear scenario of what is going on between these two proteins on individual mRNAs. We speculate that both mechanisms are taking place and that the specific mechanism of translation initiation differs for differently arranged mRNAs.

Minor comments:

(5) Figure S2C: why is there a strong reduction of the stop codon peak for 3d and 3h KDs?

We have checked the Ribowaltz profiles of all replicates (in the Supplementary data we are showing only a representative replicate I) and the stop codon peak differs a lot among the replicates. We think that this way of plotting was optimized for calculation and visualization of P-sites and triplet periodicity and thus is not suitable for this type of comparison among samples. Therefore, we have performed our own analysis where the 5’ ends of reads are used instead of P-sites and triplicates are averaged and normalized to CDS (see below please), so that all samples can be compared directly in one plot (same as Fig. S13A but for stop codon). We can see that the stop codon peak really differs and is the smallest for eIF3hKD. However, these changes are in the range of 20% and we are not sure about their biological significance. We therefore refrain from drawing any conclusions. In general, reduced stop codon peak may signal faster termination or increased stop codon readthrough, but the latter should be accompanied by an increased ribosome density in the 3’UTR, which is not the case. A defect in termination efficiency would be manifested by an increased stop codon peak, instead.

Author response image 1.

(6) Figures 5 and S8: Adding a vertical line at 'zero' in all cumulative plots will help the reader understand the author's interpretation of the data. 

We have added a dashed grey vertical line at zero as requested. However, for interpretation of these plots, the reader should focus on the colored curve and whether it is shifted in respect to the grey curve (background) or not. Shift to the right indicates increased expression, while shift to the left indicates decreased expression. The reported p-value then indicates the statistical significance of the shift.

(7) The entire Figure 2 are controls that can go to Supplementary Material. The clustering of Figure S3B could be shown in the main Figure, as it is a very easy read-out of the consistent effects of the KDs of the different eIF3 subunits under analysis.

We have moved the entire Figure 2 to Supplementary Material as suggested (the original panels can be found as Supplementary Figures 1B, 1C and 3A). Figure S3B is now the main Figure 2E. 

(8) There are 3 replicates for Ribo-Seq and four for RNA-Seq. Were these not carried out in parallel, as it is usually done in Ribo-seq experiments? Why is there an extra replicate for RNASeq?

Yes, the three replicates were carried out in parallel. We have decided to add the fourth replicate in RNA-Seq to increase the data robustness as the RNA-Seq is used for normalization of FP to calculate the TE, which was our main analyzed metrics in this article. We had the option to add the fourth replicate as we originally prepared five biological replicates for all samples, but after performing the control experiments, we selected only the 3 best replicates for the Ribo-Seq library preparation and sequencing.  

(9) Please, add another sheet in Table S2 with the names of all genes that change only at the translation (RPF) levels.

As requested, we have added three extra sheets (one for each downregulation) for differential FP with Padjusted <0.05 in the Spreadsheet S2. We also provide a complete unfiltered differential expression data (sheet named “all data”), so that readers can filter out any relevant data based on their interest.

(10) Page 5, bottom: ' ...we showed that the expression of all 12 eIF3 subunits is interconnected such that perturbance of the expression of one subunit results in the down-regulation of entire modules...'. This is not true for eIF3d, as shown in Fig1B and mentioned in Results.

This reviewer is correct. By this generalized statement, we were trying to summarize our previous results from Wagner et al., 2014, PMID: 24912683; Wagner et al.,2016, PMID: 27924037 and Herrmannova et al.,2020, PMID: 31863585. The eIF3d downregulation is the only exception that does not affect expression of any other eIF3 subunit. Therefore, we have rewritten this paragraph accordingly: “We recently reported a comprehensive in vivo analysis of the modular dynamics of the human eIF3 complex (Wagner et al, 2020; Wagner et al, 2014; Wagner et al., 2016). Using a systematic individual downregulation strategy, we showed that the expression of all 12 eIF3 subunits is interconnected such that perturbance of the expression of one subunit results in the down-regulation of entire modules leading to the formation of partial eIF3 subcomplexes with limited functionality (Herrmannova et al, 2020). eIF3d is the only exception in this respect, as its downregulation does not influence expression of any other eIF3 subunit.”

(11) Page 10, bottom: ' The PCA plot and hierarchical clustering... These results suggest that eIF3h depletion impacts the translatome differentially than depletion of eIF3e or eIF3d.' This is already obvious in the polysome profiles of Figure S2C.

We agree that this result is surely not surprising given the polysome profile and growth phenotype analyses of eIF3hKD. But still, we think that the PCA plot and hierarchical clustering results represent valuable controls. Nonetheless, we rephrased this section to note that this result agrees with the polysome profiles analysis: “The PCA plot and hierarchical clustering (Figure 2A and Supplementary Figure 4A) showed clustering of the samples into two main groups: Ribo-Seq and RNA-seq, and also into two subgroups; NT and eIF3hKD samples clustered on one side and eIF3eKD and eIF3dKD samples on the other. These results suggest that the eIF3h depletion has a much milder impact on the translatome than depletion of eIF3e or eIF3d, which agrees with the growth phenotype and polysome profile analyses (Supplementary Figure 1A and 1D).”

(12) Page 12: ' As for the eIF3dKD "unique upregulated" DTEGs, we identified one interesting and unique KEGG pathway, the ABC transporters (Supplementary Figure 5A, in green).' This sentence is confusing, as there are more pathways that are significant in this group, so it is unclear why the authors consider it 'unique'.

The eIF3dKD “unique upregulated” group comprises genes with increased TE only in eIF3dKD but not in eIF3eKD or eIF3hKD (500 genes, Fig 2G). All these 500 genes were examined for enrichment in the KEGG pathways, and the top 10 significant pathways were reported (Fig S6A). However, 8 out of these 10 pathways were also significantly enriched in other gene groups examined (e.g. eIF3d/eIF3e common). Therefore, the two remaining pathways (“ABC transporters” and “Other types of O-glycan biosynthesis”) are truly unique for eIF3dKD. We wanted to highlight the ABC transporters group in particular because we find it rather interesting (for the reasons mentioned in the article). We have corrected the sentence in question to avoid confusion: “Among the eIF3dKD “unique upregulated” DTEGs, we identified one interesting KEGG pathway, the ABC transporters, which did not show up in other gene groups (Supplementary Figure 6A, in green). A total of 12 different ABC transporters had elevated TE (9 of them are unique to eIF3dKD, while 3 were also found in eIF3eKD), 6 of which (ABCC1-5, ABCC10) belong to the C subfamily, known to confer multidrug resistance with alternative designation as multidrug resistance protein (MRP1-5, MRP7) (Sodani et al, 2012).

Interestingly, all six of these ABCC transporters were upregulated solely at the translational level (Supplementary Spreadsheet S2).”    

(13) Note typo ('Various') in Figure 4A.

Corrected

(14) The introduction could be shortened.

This is a very subjective requirement. In fact, when this manuscript was reviewed in NAR, we were asked by two reviewers to expand it substantially. Because a number of various research topics come together in this work, e.g. translational regulation, the eIF3 structure and function, MAPK/ERK signaling, we are convinced that all of them demand a comprehensive introduction for non-experts in each of these topics. Therefore, with all due respect to this reviewer, we did not ultimately shorten it.

Reviewer #2 (Recommendations For The Authors):

- In Figure 2, it would be useful to know why eIF3d is destabilized by eIF3e knockdown - is it protein degradation and why do the eIF3d/e knockdowns not more completely phenocopy each other when there is the same reduction to eIF3d as in the eIF3d knockdown sample?

Yes, we do think that protein degradation lies behind the eIF3d destabilization in the eIF3eKD, but we have not yet directly demonstrated this. However, we have shown that eIF3d mRNA levels are not altered in eIF3eKD and that Ribo-Seq data indicate no change in TE or FP for eIF3d-encoding mRNA in eIF3eKD. Nonetheless, it is important to note (and we discuss it in the article) that eIF3d levels in eIF3dKD are lower than eIF3d levels in eIF3eKD (please see Supplementary Figure 1C). In fact, we believe that this is one of the main reasons for the eIF3d/e knockdowns differences.

- The western blots in Figures 4 and 6 show modest changes to target protein levels and would be strengthened by quantification.

We have added the quantifications as requested by this reviewer and the reviewer 3.

- For Figure 4, this figure would be strengthened by experiments showing if the increase in ribosomal protein levels is correlated with actual changes to ribosome biogenesis.

As suggested, we performed polysome profiling in the presence of EDTA to monitor changes in the 60S/40S ratio, indicating a potential imbalance in the biogenesis of individual ribosome subunits. We found that it was not affected (Figure 3G). In addition, we performed the same experiment, normalizing all samples to the same number of cells (cells were carefully counted before lysis). In this way, we confirmed that eIF3dKD and eIF3eKD cells indeed contain a significantly increased number of ribosomes, in agreement with the western blot analysis (Figure 3H).

- In Figure 6, there needs to be a nuclear loading control.

This experiment was repeated with Lamin B1 used as a nuclear loading control – it is now shown as Fig. 5F.

- For Figure 8, these findings would be strengthened using luciferase reporter assays where the various RNA determinants are experimentally tested. Similarly, 5′ TOP RNA reporters would have been appreciated in Figure 4.

This is indeed a logical continuation of our work, which represents the current work in progress of one of the PhD students. We apologize, but we consider this time- and resource-demanding analysis out of scope of this article.

Reviewer #3 (Recommendations For The Authors):

(1) Within the many effects observed, it is mentioned that eIF3d is known to be overexpressed while eIF3e is underexpressed in many cancers, but knockdown of either subunit decreases MDM2 levels, which would be expected to increase P53 activity and decrease tumor cell transformation. In contrast, they also report that 3e/3d knockdown dramatically increases levels of cJUN, presumably due to increased MAPK activity, and is expected to increase protumor gene expression. Additional discussion is needed to clarify the significance of the findings, which are a bit confusing.

This is indeed true. However, considering the complexity of eIF3, the largest initiation factor among all, as well as the broad portfolio of its functions, it is perhaps not so surprising that the observed effects are complex and may seem even contradictory in respect to cancer. To acknowledge that, we expanded the corresponding part of discussion as follows: “Here, we demonstrate that alterations in the eIF3 subunit stoichiometry and/or eIF3 subcomplexes have distinct effects on the translatome; for example, they affect factors that play a prominent (either positive or negative) role in cancer biology (e.g., MDM2 and cJUN), but the resulting impact is unclear so far. Considering the complex interactions between these factors as well as the complexity of the eIF3 complex per se, future studies are required to delineate the specific oncogenic and tumor suppressive pathways that play a predominant role in mediating the effects of perturbations in the eIF3 complex in the context of neoplasia.”

(2) There are places in the text where the authors refer to changes in transcriptional control when RNA levels differ, but transcription versus RNA turnover wasn't tested, e.g. page 16 and Figure S10, qPCR does not confirm "transcriptional upregulation in all three knockdowns" and page 19 "despite apparent compensatory mechanisms that increase their transcription."

This is indeed true, the sentences in question were corrected. The term “increased mRNA levels” was used instead of transcriptional upregulation (increased mRNA stabilization is also possible).

(3) Similarly, the authors suggest that steady-state LARP1 protein levels are unaffected based on ribosome footprint counts (page 21). It is incorrect to assume this, because ribosome footprints can be elevated due to stalling on RNA that isn't being translated and doesn't yield more protein, and because levels of translated RNA/synthesized proteins do not always reflect steady-state protein levels, especially in mutants that could affect lysosome levels and protein turnover. Also page 12, 1st paragraph suggests protein production is down when ribosome footprints are changed.

Yes, we are well-aware of this known limitation of Ribo-seq analysis. Therefore, the steadystate protein levels of our key hits were verified by western blotting. In addition, we have removed the sentence about LARP1 because it was based on Ribo-Seq data only without experimental evaluation of the steady-state LARP1 protein levels.

(4) The translation buffering effect is not clear in some Figures, e.g. S6, S8, 8A, and B. The authors show a scheme for translationally buffered RNAs being clustered in the upper right and lower left quadrants in S4H (translation up with transcript level down and v.v.), but in the FP versus RNA plots, the non-TOP RNAs and 4E-P-regulated RNAs don't show this behavior, and appear to show a similar distribution to the global changes. Some of the right panels in these figures show modest shifts, but it's not clear how these were determined to be significant. More information is needed to clarify, or a different presentation, such as displaying the RNA subsets in the left panels with heat map coloring to reveal whether RNAs show the buffered translation pattern defined in purple in Figure S4H, or by reporting a statistical parameter or number of RNAs that show behavior out of total for significance. Currently the conclusion that these RNAs are translationally buffered seems subjective since there are clearly many RNAs that don't show changes, or show translation-only or RNA-only changes.

We would like to clarify that S4H does not indicate a necessity for changes in FPs in the buffered subsets. Although opposing changes in total mRNA and FPs are classified as buffering, often we also consider the scenario where there are changes to the total mRNA levels not accompanied by changes in ribosome association.

In figure S6, the scatterplots indicate a high density of genes shifted towards negative fold changes on the x-axis (total mRNA). This is also reflected in the empirical cumulative distribution functions (ecdfs) for the log2 fold changes in total mRNA in the far right panels of A and B, and the lack of changes in log2 fold change for FPs (middle panels). Similarly, in figure S8, the scatterplots indicate a density of genes shifted towards positive fold changes on the x-axis for total mRNA. The ecdfs also demonstrate that there is a significant directional shift in log2 fold changes in the total mRNA that is not present to a similar degree in the FPs, consistent with translational offsetting. It is rightly pointed out that not all genes in these sets follow the same pattern of regulation. We have revised the title of Supplementary Figure S6 (now S7) to reflect this. However, we would like to emphasize that these figures are not intended to communicate that all genes within these sets of interest are regulated in the same manner, but rather that when considered as a whole, the predominant effect seen is that of translational offsetting (directional shifts in the log2 fold change distribution of total mRNA that are not accompanied by similar shifts in FP mRNA log2 fold changes).

The significance of these differences was determined by comparing the ecdfs of the log2 fold changes for the genes belonging to a particular set (e.g. non-TOP mTOR-sensitive, p-eIF4E-sensitive) against all other expressed genes (background) using a Wilcoxan rank sum test. This allows identification of significant shifts in the distributions that have a clear directionality (if there is an overall increase, or decrease in fold changes of FPs or total mRNA compared to background). If log2 fold changes are different from background, but without a clear directionality (equally likely to be increased or decreased), the test will not yield a significant result. This approach allows assessment of the overall behavior of gene signatures within a given dataset in a manner that is completely threshold-independent, such that it does not rely on classification of genes into different regulatory categories (translation only, buffering, etc.) based on significance or fold-change cut-offs (as in S4H). Therefore, we believe that this unbiased approach is well-suited for identifying cases when there are many genes that follow similar patterns of regulation within a given dataset.

(5) Page 10-"These results suggest that eIF3h depletion impacts the translatome differentially than depletion of eIF3e or eIF3d" ...These results suggest that eIF3h has less impact on the translatome, not that it does so differently. If it were changing translation by a different mechanism, I would not expect it to cluster with control.

This sentence was rewritten as follows: “The PCA plot and hierarchical clustering (Figure 2A and Supplementary Figure 4A) showed clustering of the samples into two main groups: RiboSeq and RNA-seq, and also into two subgroups; NT and eIF3hKD samples clustered on one side and eIF3eKD and eIF3dKD samples on the other. These results suggest that the eIF3h depletion has a much milder impact on the translatome than depletion of eIF3e or eIF3d, which agrees with the growth phenotype and polysome profile analyses (Supplementary Figure 1A and 1D).”

Other minor issues:

(1) There are some typos: Figure 2 leves, Figure 4 variou,

Corrected.

(2) Figure 3, font for genes on volcano plot too small

Yes, maybe, however the resolution of this image is high enough to enlarge a certain part of it at will. In our opinion, a larger font would take up too much space, which would reduce the informativeness of this graph.

(3) Figure S5, highlighting isn't defined.

The figure legend for S5A (now S6A) states: “Less significant terms ranking 11 and below are in grey. Terms specifically discussed in the main text are highlighted in green.” Perhaps it was overlooked by this reviewer.

(4) At several points the authors refer to "the MAPK signaling pathway", suggesting there is a single MAPK that is affected, e.g in the title, page 3, and other places when it seems they mean "MAPK signaling pathways" since several MAPK pathways appear to be affected.

We apologize for any terminological inaccuracies. There are indeed several MAPK pathways operating in cells. In our study, we focused mainly on the MAPK/ERK pathway. The confusion probably stems from the fact that the corresponding term in the KEGG pathway database is labeled "MAPK signaling pathway" and this term, although singular, includes all MAPK pathways. We have carefully reviewed the entire article and have corrected the term used accordingly to either: 1) MAPK pathways in general, 2) the MAPK/ERK pathway for this particular pathway, or 3) "MAPK signaling pathway", where the KEGG term is meant.

(5) Some eIF3 subunit RNAs have TOP motifs. One might expect 3e and 3h levels to change as a function of 3d knockdown due to TOP motifs but this is not observed. Can the authors speculate why the eIF3 subunit levels don't change but other TOP RNAs show TE changes? Is this true for other translation factors, or just for eIF3, or just for these subunits? Could the Western blot be out of linear range for the antibody or is there feedback affecting eIF3 levels differently than the other TOP RNAs, or a protein turnover mechanism to maintain eIF3 levels?

This is indeed a very interesting question. In addition to the mRNAs encoding ribosomal proteins, we examined all TOP mRNAs and added an additional sheet to the S2 supplemental spreadsheet with all TOP RNAs listed in (Philippe et al., 2020, PMID: 32094190). According to our Ribo-Seq data, we could expect to see increased protein levels of eIF3a and eIF3f in eIF3dKD and eIF3eKD, but this is not the case, as judged from extensive western blot analysis performed in (Wagner et. al 2016, PMID: 27924037). Indeed, we cannot rule out the involvement of a compensatory mechanism monitoring and maintaining the levels of eIF3 subunits at steady-state – increasing or decreasing them if necessary, which could depend on the TOP motif-mediated regulation. However, we think that in our KDs, all non-targeted subunits that lose their direct binding partner in eIF3 due to siRNA treatment become rapidly degraded. For example, co-downregulation of subunits d, k and l in eIF3eKD is very likely caused by protein degradation as a result of a loss of their direct binding partner – eIF3e. Since we showed that the yeast eIF3 complex assembles co-translationally (Wagner et. al 2020, PMID: 32589964), and there is no reason to think that mammalian eIF3 differs in this regard, our working hypothesis is that free subunits that are not promptly incorporated into the eIF3 complex are rapidly degraded, and the presence or absence of the TOP motif in the 5’ UTR of their mRNAs has no effect. As for the other TOP mRNAs, translation factors eEF1B2, eEF1D, eEF1G, eEF2 have significantly increased FPs in both eIF3dKD and eIF3eKD, but we did not check their protein levels by western blotting to conclude anything specific.

Author Response

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

Major change:

All three of our reviewers raised the possibility that changes in movement during the time spent at the center ports could have contributed to changes in SWR rates. Analyses to address this possibility, based on the examination of trials with high and low speeds, were originally included in the supplement but we did not sufficiently highlight and explain these results. To rectify this, we have moved these results into a new main Figure 3 and now include a paragraph describing our interpretation of these results (page 9). We also include a more detailed description of the subjects’ behavior during port times – namely, that all subjects must remain quite stationary while at the reward ports in order to keep their nose in a specific position which keeps the port triggered. As a result, all subjects maintain head speeds well below our typical speed threshold for immobility while at the ports. This leads us to predict that any feedback based on periods of immobility alone (as requested by Reviewer 3) would show results very similar to our Control cohort and would not alter SWR rates seen during neurofeedback trials.

Minor changes:

(1) Reviewer 1 observed our that reported statistics appeared to be missing an interaction term showing that neurofeedback differentially affected the SWR rate/count pre- and postreward. We apologize for a lack of clarity here: we fit pre- and post-reward times with separate linear mixed effects models, so this interaction term is neither expected nor defined in our model. We have added a sentence clarifying this aspect of our LME approach in the Methods section: “Each model is designed to compare samples from all trials of the control group to samples from neurofeedback and delay trials from the neurofeedback cohort for a specific time period (for instance, pre-reward-delivery at the center ports).” Combining both times in the same model would require adding an additional hierarchical level in order to preserve the pairing of the pre- and post-reward time period for each trial, which we are concerned would complicate the formulation and interpretation of the model. However, the reviewer raises a good point that the comparison between these two time periods reveals an additional difference between the trial types: SWR rate remains relatively consistent between the pre- and post-reward periods during neurofeedback trials, while delay and control trials show a clear increase in SWR rate between the two time periods. To visualize and quantify this effect, we calculated the difference in SWR rates between the two time periods and now include this plot as Supplementary Figure 2F, which is referenced in page 8 of the main text.

(2) Reviewer 2 found our original title, “Neurofeedback training can modulate task-relevant memory replay in rats” to be misleading and suggestive of a manipulation to memory content. We are in complete agreement with the Reviewer in that our manipulation does not alter replay content, so to be more specific and accurate, we have changed our title to their suggestion “Neurofeedback training can modulate task-relevant memory replay rate in rats” accordingly.

(3) Reviewer 2 also requested that we include analyses quantifying baseline SWR rates for each of our experimental subjects. Although we initially considered reporting our results in measures of change relative to each individual animal’s baseline, we decided against this approach for several reasons.

First, it is important to clarify that we extensively train the animals on the task prior to implant, so we do not have access to a truly naïve, pre-behavior baseline SWR rate for any of our subjects. However, because the pre-implant training is conducted consistently between our neurofeedback and our control cohort, we have no reason to believe that the behavioral training prior to implant would introduce differences in SWR rate between the cohorts. Indeed, we find no difference in post-reward SWR rate (or SWR rate at the home well) when we quantify the first 250 trials of post-implant behavior for each subject (see panel A below). Note that we cannot compare the pre-reward SWR rate at this point, because it is influenced by the task structure which guarantees at least one SWR in each neurofeedback trial pre-reward.

Further, we do find that SWR rate is quite consistent over many days of task performance in the control cohort (show for the post-reward period in panel B below). This suggests that comparing the post-neurofeedback training SWR rates for the neurofeedback cohort to SWR rates throughout the training for the control cohort is not likely to be confounded by differing amounts of training experience. This is supported by our analyses in Figure 2 which show no differences in SWR rate between the two cohorts when considering pre- and post-reward times combined.

Author response image 1.

(A) SWR rate calculated during the post-reward period at the center port for the first 250 trials of postimplant behavior for each animal. Trials of all types are included (ie both neurofeedback trials and delay trials for the manipulation cohort). Groupwise comparison p=0.192. (B) Mean SWR rate during the post-reward period at the center port for each behavioral training epoch shows no systematic change over time across subjects within the control cohort.

Finally, within each cohort, we found the overall SWR rates to be quite consistent across animals. If each subject in the neurofeedback cohort had shown dramatically different SWR rates at the beginning of neurofeedback training, we would have needed to express the effect of neurofeedback training relative to baseline for each animal. However, since the range of SWR rates were highly comparable, we felt that it was more accessible, and easier to place our results within the context of the literature, by expressing our results as simple SWR rates themselves rather than measures of relative change. Within the neurofeedback cohort, comparing neurofeedback to delay trials is inherently matched for baseline SWR rate since these comparisons are made within the same animal.

(4) Finally, Reviewer 2 raises the possibility that older animals or those with cognitive deficits might respond to neurofeedback differently. We entirely agree with this possibility, and note this in our Discussion section: “Since the neurofeedback paradigm depends on the occurrence of at least a low endogenous rate of SWR occurrence, it would be important to implement neurofeedback training as a relatively early interventional strategy prior to extensive neurodegeneration, and training may take longer in aged or impaired subjects.”

Author response:

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

Reviewer #1

(1) In the "Introduction" section, an important aspect that requires attention pertains to the discussion surrounding the heterodimerization of CXCR4 and CCR5. Notably, the manuscript overlooks a recent study (https://doi.org/10.1038/s41467-023-42082-z) elucidating the mechanism underlying the formation of functional dimers within these G protein-coupled receptors (GPCRs)…The inclusion of this study within the manuscript would significantly enrich the contextual framework of the work, offering readers a comprehensive understanding of the current knowledge surrounding the structural dynamics and functional implications of CXCR4 and CCR5 heterodimerization.

We thank the reviewer for his/her recommendation to enrich the contextual framework of our study. The Nature Communications paper by Di Marino et al. was published after we sent the first version of our manuscript to eLife, and therefore was not included in the discussion. As the reviewer rightly indicates, this paper elucidates the mechanism underlying the formation of functional dimers within CCR5 and CXCR4. Using metadynamics approaches, the authors emphasize the importance of distinct transmembrane regions for dimerization of the two receptors. In particular, CXCR4 shows two low energy dimer structures and the TMVI-TMVII helices are the preferred interfaces involved in the protomer interactions in both cases. Although the study uses in silico techniques, it also includes the molecular binding mechanism of CCR5 and CXCR4 in the membrane environment, as the authors generate a model in which the receptors are immersed in a 1-palmitoyl-2-oleoyl-sn-glycero-3-phosphocholine (POPC) phospholipid bilayer with 10% cholesterol. This is an important point in this study, as membrane lipids also interact with membrane proteins, and the lipid composition affects CXCR4 oligomerization (Gardeta S.R. et al. Front. Immunol. 2023). In particular, Di Marino et al. find a cholesterol molecule placed in-between the two CXCR4 protomers where it engages a series of hydrophobic interactions with residues including Leu132, Val214, Leu216 and Phe249. Then, the polar head of cholesterol forms an H-bond with Tyr135 that further stabilizes protomer binding. In our hands, the F249L mutation in CXCR4 reverted the antagonism of AGR1.137, suggesting that the compound binds, among others, this residue. We should, nonetheless, indicate that we analyzed receptor oligomerization and not CXCR4 dimerization, which was the main object of the Di Marino et al. study. It is therefore also plausible that other residues than those described as essential for CXCR4 dimerization might participate in receptor oligomerization. We can speculate that AGR1.137 might affect cholesterol binding to CXCR4 and, therefore, alter dimerization/oligomerization. Additionally, the CXCR4 x-ray structure with PDB code 3ODU (Wu B. et al. Science, 2010) experimentally shows the presence of two fatty acid molecules in contact with both TMV and TMVI. These molecules closely interact with hydrophobic residues in the protein, thereby stabilizing it in a hydrophobic environment. Although more experiments will be needed to clarify the mechanism involved, our results suggest that cholesterol and/or other lipids also play an important role in CXCR4 oligomerization and function, as seen for other GPCRs (Jakubik J. & ElFakahani E.E. Int J Mol Sci. 2021). However, we should also consider that other factors not included in the analysis by Di Marino et al. can also affect CXCR4 oligomerization; for instance, the co-expression of other chemokine receptors and/or other GPCRs that heterodimerize with CXCR4 might affect CXCR4 dynamics at the cell membrane, similar to other membrane proteins such as CD4, which also forms complexes with CXCR4 (Martinez-Muñoz L. et al. Mol. Cell 2018).

The revised discussion contains references to the study by Di Marino et al. to enrich the contextual framework of our data.

(2) In "various sections" of the manuscript, there appears to be confusion surrounding the terminology used to refer to antagonists. It is recommended to provide a clearer distinction between allosteric and orthosteric antagonists to enhance reader comprehension. An orthosteric antagonist typically binds to the same site as the endogenous ligand, directly blocking its interaction with the receptor. On the other hand, an allosteric antagonist binds to a site distinct from the orthosteric site, inducing a conformational change in the receptor that inhibits the binding of the endogenous ligand. By explicitly defining the terms "allosteric antagonist" and "orthosteric antagonist" within the manuscript, readers will be better equipped to discern the specific mechanisms discussed in the context of the study.

The behavior of the compounds described in our manuscript (AGR1.35 and AGR1.137) fits with the definition of allosteric antagonists, as they bind on a site distinct from the orthosteric site, although they only block some ligand-mediated functions and not others. This would mean that they are not formally antagonists and should be not considered as allosteric compounds, as their binding on CXCR4 does not alter CXCL12 binding, although they might affect its affinity. In this sense, our compounds respond much better to the concept of negative allosteric modulators (Gao Z.-G. & Jacobson K.A. Drug Discov. Today Technol. 2013). They act by binding on a site distinct from the orthosteric site and selectively block some downstream signaling pathways but not others induced by the same endogenous agonist.

To avoid confusion and to clarify the role of the compounds described in this study, we now refer to them as negative allosteric modulators along the manuscript.

(3) In the Results section, the computational approach employed for "screening small compounds targeting CXCR4, particularly focusing on the inhibition of CXCL12-induced CXCR4 nanoclustering", requires clarification due to several points of incomprehension. The following recommendations aim to address these concerns and enhance the overall clarity of the section:

(1) Computational Approach and Binding Mode Description: 

-Explicitly describe the methodology for identifying the pocket/clef area in angstroms (Å) on the CXCR4 protein structure. Include details on how the volume of the cleft enclosed by TMV and TMVI was determined, as this information is not readily apparent in the provided reference (https://doi.org/10.1073/pnas.1601278113).

The identification of the cleft was based on the observations by Wu et al. (Wu B. et al. Science 2010) who described the presence of bound lipids in the area formed by TMV and VI, and those of Wescott et al. (Wescott M.P. et al. Proc. Natl. Acad. Sci. 2016) on the importance of TMVI in the transmission of conformational changes promoted by CXCL12 on CXCR4 towards the cytoplasmic surface of the receptor to link the binding site with signaling activation. Collectively, these results, and our previous data on the critical role of the N-terminus region of TMVI for CXCR4 oligomerization (Martinez-Muñoz L. et al. Mol. Cell 2018), focused our in silico screening to this region. Once we detected that several compounds bound CXCR4 in this region, the cleavage properties were calculated by subtracting the compound structure. The resulting PDB was analyzed using the PDBsum server (Laskowski R.A. et. al. Protein Sci. 2018). Volume calculations were obtained using the server analyzing surface clefts by SURFNET (Laskowski R. A. J. Mol. Graph. 1995). The theoretical interaction surface between the selected compounds and CXCR4 and the atomic distances between the protein residues and the compounds was calculated using the PISA server (Krissinel E. & Henrick K. J. Mol. Biol. 2007) (Fig. I, only for review purposes). The analysis of the cleft occupied by AGR1.135 showed two independent cavities of 434 Å3 and 1,381 Å3 that were not connected to the orthosteric site. In the case of AGR1.137, the data revealed two distinct clefts of 790 Å3 and 580 Å3 (Fig. I, only for review purposes). These details have been included in the revised manuscript (New Fig. 1A, Supplementary Fig 8A, B).

(4) Clarify the statement regarding the cleft being "surface exposed for interactions with the plasma membrane," particularly in the context of its embedding within the membrane.

For GPCRs, transmembrane domains represent binding sites for bioactive lipids that play important functional and physiological roles (Huwiler A. & Zangemeister-Wittke U. Pharmacol. Ther. 2018). The channel between TMV and TMVI connects the orthosteric chemokine binding pocket to the lipid bilayer and is occupied by an oleic acid molecule, according to the CXCR4 structure published in 2010 (Wu B. et al. Science 2010). In addition, the target region contains residues involved in cholesterol (and perhaps other lipids) engagement (Di Marino et al. Nat. Commun. 2023). Taken together, these data support our statement that the cleft supports interactions between CXCR4 molecules and the plasma membrane. 

Moreover, the data of Di Marino et al. also support that CCR5 and CXCR4 have a symmetric and an asymmetric binding mode. Therefore, either dimeric structure has the possibility to form trimers, tetramers, and even oligomers by using the free binding interface to complex with another protomer. This hypothesis suggests that the interaction of dimers to form oligomers should involve residues distinct from those included in the dimeric conformation.

The sentence has been modified in the revised manuscript to clarify comprehension.

(5) Discuss the rationale behind targeting the allosteric binding pocket instead of the orthosteric pocket, outlining potential advantages and disadvantages.

The advantages and disadvantages of using negative allosteric modulators vs orthosteric antagonists have been now included in the revised discussion. 

The majority of GPCR-targeted drugs function by binding to the orthosteric site of the receptor, and are agonists, partial agonists, antagonists or inverse agonists. These orthosteric compounds can have off-target effects and poor selectivity due to highly homologous receptor orthosteric sites and to abrogation of spatial and/or temporal endogenous signaling patterns. 

The alternative is to use allosteric modulators, which can tune the functions associated with the receptors without affecting the orthosteric site. They can be positive, negative or neutral modulators, depending on their effect on the functionality of the receptor (Foster D.J. & Conn P.J. Neuron 2017). For example, the use of a negative allosteric modulator of a chemokine receptor to dampen pathological signaling events, while retaining full signaling for non-pathological activities might limit adverse effects (Kohout T.A.et al. J. Biol. Chem. 2004). In this case, the negative allosteric modulator 873140 blocks CCL3 binding on CCR5 but does not alter CCL5 binding (Watson C. et al. Mol. Pharmacol. 2005). In other cases, allosteric modulators can stabilize a particular receptor conformation and block others. The mechanism of action of the anti-HIV-1, FDAapproved, CCR5 allosteric modulator, maraviroc (Jin J. et al. Sci. Signal. 2018) is attributed to its ability to modulate CCR5 dimer populations and their subsequent subcellular trafficking and localization to the cell membrane (Jin J .et al. Sci. Signal. 2018). Two CCR5 dimeric conformations that are imperative for membrane localization were present in the absence of maraviroc; however, an additional CCR5 dimer conformation was discovered after the addition of maraviroc, and all homodimeric conformations were further stabilized. This finding is consistent with the observation that CCR5 dimers and oligomers inhibit HIV host-cell entry, likely by preventing the HIV-1 co-receptor formation.

It is well known that GPCRs activate G proteins, but they also recruit additional proteins (e.g., β-arrestins) that induce signaling cascades which, in turn, can direct specific subsets of cellular responses independent of G protein activation (Eichel K. et al. Nature 2018) and are responsible for either therapeutic or adverse effects. Allosteric modulators can thus be used to block these adverse effects without influencing the therapeutic benefits. This was the case in the design of G protein-biased agonists for the kappa opioid receptor, which maintain the desirable antinociceptive and antipruritic effects and eliminate the sedative and dissociative effects in rodent models (Brust T.F. et al. Sci. Signal 2016).

(6) Provide the PDB ID of the CXCR4 structure used as a template for modeling with SwissModel. Explain the decision to model the structure from the amino acid sequence and suggest an alternative approach, such as utilizing AlphaFold structures and performing classical molecular dynamics with subsequent clustering for the best representative structure.

The PDB used as a template for modeling CXCR4 was 3ODU. This information was already included in the material and methods section. At the time we performed these analyses, there were several crystallographic structures of CXCR4 in complex with different molecules and peptides deposited at the PDB. None of them included a full construct containing the complete receptor sequence to provide a suitable sample for Xray structure resolution, as the N- and C-terminal ends of CXCR4 are very flexible loops. In addition, the CXCR4 constructs contained T4 lysozyme inserted between helices TMV and TMVI to increase the stability of the protein––a common strategy used to facilitate crystallogenesis of GPCRs (Zou Y. et al. PLoS One 2012). Therefore, we generated a CXCR4 homology model using the SWISS-MODEL server (Waterhouse A. et al. Nucleic Acids Res. 2018). This program reconstructed the loop between TMV and TMVI, a domain particularly important in this study that was not present in any of the crystal structure available in PDB. The model structure was, nonetheless, still incomplete, as it began at P27 and ended at S319 because the terminal ends were not resolved in the crystal structure used as a template. Nevertheless, we considered that these terminal ends were not involved in CXCR4 oligomerization. 

As Alphafold was not available at the time we initiated this project, we didn’t use it. However, we have now updated our workflow to current methods and predicted the structure of the target using AlphaFold (Jumper J. et al. Nature 2021) and the sequence available under UniProt entry P61073. We prepared the ligands using OpenBabel (O’Boyle N.M. et al., J. Cheminformatics 2011), with a gasteiger charge assignment, and generated 10 conformers for each input ligand using the OpenBabel genetic algorithm. We then prepared the target structure with Openmm, removing all waters and possible heteroatoms, and adding all missing atoms. We next predicted the target binding pockets with fPocket (Le Guilloux V. et al. BMC Bioinformatics 2009), p2rank (Krivak R. & Hoksza, J. Cheminformatics 2018), and AutoDock autosite (Ravindranath P.A. & Sanner M.F. Bioinformatics 2016). We chose only those pockets between TMV and TMVI (see answer to point 3). We merged the results of the three programs into so-called consensus pockets, as two pockets are said to be sufficiently similar if at least 75% of their surfaces are shared (del Hoyo D. et al. J. Chem. Inform. Model. 2023). From the consensus pockets, there was one pocket that was significantly larger than the others and was therefore selected. We then docked the ligand conformers in this pocket using AutoDock GPU (Santos-Martins D. et al. J. Chem. Theory Comput. 2021), LeDock (Liu N & Xu Z., IOP Conf. Ser. Earth Environ. Sci. 2019), and Vina (Eberhardt J. et al. J. Chem. Inf. Model. 2021). The number of dockings varied from 210 to 287 poses. We scored each pose with the Vina score using ODDT (Wójcikowski M. et al. J. Cheminform. 2015). Then, we clustered the different solutions into groups whose maximum RMSD was 1Å. This resulted in 40 clusters, the representative of each cluster was the one with maximum Vina score and confirmed that the selected compounds bound this pocket (Author response image 1). When required, we calculated the binding affinity using Schrodinger’s MM-GBSA procedure (Greenidge P.A. et al. J. Chem. Inf. Model. 2013), in two ways: first, assuming that the ligand and target are fixed; second, with an energy minimization of all the atoms within a distance of 3Å from the ligand. This information has now been included in the revised version of the manuscript.

Author response image 1.

AGR1.135 docking in CXCR4 using the updated protocol for ligand docking. Cartoon representation colored in gray with TMV and TMVI shown in blue and pink, respectively. AGR1.135 is shown in stick representation with carbons in yellow, oxygens in red and nitrogens in blue.

(7) Specify the meaning of "minimal interaction energy" and where (if present) the interaction scores are reported in the text.

We refer to minimal interaction energy, the best docking score, that is, the best score obtained in our docking studies. These data were not included in the previous manuscript due to space restrictions but are now included in the reviewed manuscript.

(8) You performed docking studies using GLIDE to identify potential binding sites for the small compounds on the CXCR4 protein. The top-scoring binders were then subjected to further refinement using PELE simulations. However, I realize that a detailed description of the specific binding modes of these compounds was not provided in the text. Please make the description of binding poses more detailed

Firstly, to assess the reliability of this method, a PELE study was carried out for the control molecule IT1t, which is a small drug-like isothiourea derivative that has been crystallized in complex with CXCR4 (PDB code: 3ODU). IT1t is a CXCR4 antagonist that binds to the CXCL12 binding cavity and inhibits HIV-1 infection (Das D. Antimicrob. Agents Chemother. 2015; Dekkers S. et al. J. Med. Chem. 2023). From the best five trajectories, two of them had clearly better binding energies, and corresponded to almost the same predicted pose of the molecule. Although the predicted binding mode was not exactly the same as the one in the crystal structure, the approximation was very good, giving validation to the approach. Although PELE is a suitable technique to find potential binding sites, the predicted poses must be subsequently refined using docking programs.

Analyzing the best trajectories for the remaining ligands, at least one of the best-scored poses was always located at the orthosteric binding site of CXCR4. Even though these poses showed good binding energies, they were discarded as the in vitro biological experiments indicated that the compounds were unable to block CXCL12 binding or CXCL12-mediated inhibition of cAMP release or CXCR4 internalization. Collectively, these data indicated that the selected compounds did not behave as orthosteric inhibitors of CXCR4. The CXCL12 binding pocket is the biggest cavity in CXCR4, and so PELE may tend to place the molecules near it. However, all the compounds presented other feasible binding sites with a comparable binding energy.

AGR1.135 and AGR1.137 showed interesting poses between TMV and TMVI with very good binding energy (-51.4 and -37.2 kcal/mol, respectively). This was precisely the region we had previously selected for the in silico screening, as previously described (see response to point 3).

AGR1.131 showed two poses with low binding energy that were placed between helices TMI and TMVII (-43.6 kcal/mol) and between helices TMV and TMVI (-39.8 kcal/mol). This compound was unable to affect CXCL12-mediated chemotaxis and was therefore used as an internal negative control as it was selected in the in silico screening with the same criteria as the other compounds but failed to alter any CXCL12-mediated functions. PELE studies nonetheless provided different binding sites for each molecule, which had to be further studied using docking to obtain a more accurate binding mode. In agreement with the previous commentary, we repeated the analysis using AlphaFold and the rest of the procedure described (see our response to point 6) and calculated the binding energies for all the compounds using Schrodinger’s MM-GBSA procedure (Greenidge P.A. et al. J. Chem. Inf. Model. 2013). Calculations were performed in two ways: first, assuming that the ligand and target are fixed; second, with an energy minimization of all the atoms within a distance of 3Å from the ligand. The results using the first method indicated that AGR1.135 and AGR1.137 showed poses between TMV and TMVI with - 56.4 and -62.4 kcal/mol, respectively and AGR1.131 had a pose between TMI and TMVII with -61.6kcal/mol.  In the second method AGR1.135 and AGR1.137 showed poses between TMV and TMVI with -57.9, and -67.6 kcal/mol, respectively, and AGR1.131 of -62.2 kcal/mol between TMI and TMVII.

This information is now included in the text.

(9) (2) Experimental Design:-Justify the choice of treating Jurkat cells with a concentration of 50 μM of the selected compound. Consider exploring different concentrations and provide a rationale for the selected dosage. Additionally, clearly identify the type of small compound used in the initial experiment.

The revised version contains a new panel in Fig. 1B to show a more detailed kinetic analysis with different concentrations (1-100 µM) of the compounds in the Jurkat migration experiments. In all cases, 100 µM nearly completely abrogated cell migration, but in order to reduce the amount of DMSO added to the cells we selected 50 µM for further experiments, as it was the concentration that inhibits 50-75% of ligand-induced cell migration. Regarding the type of small compounds used in the initial experiments, they were compounds included in the library described in reference #24 (Sebastian-Pérez V. et al Med. Biol. Chem. 2017), which contains heterocyclic compounds. We would note that we do not consider AGR1.137 a final compound. We think that there is scope to develop AGR1.137-based second-generation compounds with greater solubility in water, greater specificity or affinity for CXCR4, and to evaluate delivery methods to hopefully increase activity.  

(10) Avoid reporting details in rounded parentheses within the text; consider relocating such information to the Materials and Methods section or figure captions for improved readability.

Most of the rounded parentheses within the text have been eliminated in the revised version of the manuscript to improve readability.

(11) Elaborate on the virtual screening approach using GLIDE software, specifying the targeted site and methodology employed.

For the virtual screening, we used the Glide module (SP and XP function scoring) included in the Schrödinger software package, utilizing the corresponding 3D target structure and our MBC library (Sebastián-Pérez V et al. J. Chem. Inf. Model. 2017).  The center of the catalytic pocket was selected as the centroid of the grid. In the grid generation, a scaling factor of 1.0 in van der Waals radius scaling and a partial charge cutoff of 0.25 were used. A rescoring of the SP poses of each compound was then performed with the XP scoring function of the Glide. The XP mode in Glide was used in the virtual screening, the ligand sampling was flexible, epik state penalties were added and an energy window of 2.5 kcal/mol was used for ring sampling. In the energy minimization step, the distance-dependent dielectric constant was 4.0 with a maximum number of minimization steps of 100,000. In the clustering, poses were considered as duplicates and discarded if both RMS deviation is less than 0.5 Å and maximum atomic displacement is less than 1.3 Å.

(12) Provide clarity on the statement that AGR1.131 "theoretically" binds the same motif, explaining the docking procedure used for this determination.

In the in silico screening, AGR1.131 was one of the 40 selected compounds that showed, according to the PELE analysis (see answer to point 8), a pose with low binding energy (-39.8 kcal/mol) between TMV and TMVI helices, which is the selected area for the screening. It, nonetheless, also showed a best pose placed between helices TM1 and TM7 (-43.7 kcal/mol) using the initial workflow. In conclusion, although AGR1.131 also faced to the TMV-TMVI, the most favorable pose was in the area between TMI and TMVII. In addition, the compound was included in the biological screening, where it did not affect CXCL12-mediated chemotaxis. We thus decided to use it as an internal negative control, as it has a skeleton very similar to AGR1.135 and AGR1.137 and can interact with the TM domains of CXCR4 without promoting biological effects. This statement has been clarified in the revised text.

(13) Toxicity Testing:

-Enhance the explanation of the approach to testing the toxicity of the compound in Jurkat cells. Consider incorporating positive controls to strengthen the assessment and clarify the experimental design.

All the selected compounds in the in silico screening were initially tested for propidium iodide incorporation in treated cells in a toxicity assay, and some of them were discarded for further experiments (e.g., AGR1.103 and VSP3.1).

Further evaluation of Jurkat cell viability was determined by cell cycle analysis using propidium iodide.  Supplementary Fig. 1B included the percentage of each cell cycle phase, and data indicated no significant differences between the treatments tested. Nevertheless, at the suggestion of the reviewer, and to clarify this issue, positive controls inducing Jurkat cell death (staurosporine and hydrogen peroxide) have also been included in the new Supplementary Fig. 2. The new figure also includes a table showing the percentage of cells in each cell-cycle phase.  

(14) In the Results section concerning "AGR1.135 and AGR1.137 blocking CXCL12-mediated CXCR4 nanoclustering and dynamics", several points can be improved to enhance clarity and coherence: 1. Specificity of Low Molecular Weight Compounds:  

-Clearly articulate how AGR1.135 and AGR1.137 specifically target homodimeric CXCR4 and provide an explanation for their lack of impact on heterodimeric CXCR4-CCR5 in that region.

First of all, we should clarify that when we talk about receptor nanoclustering, oligomers refer to complexes including 3 or more receptors and, therefore, the residues involved in these interactions can differ from those involved in receptor dimerization. Moreover, our FRET experiments did not indicate that the compounds alter receptor dimerization (see new Supplementary Fig. 7). Of note, mutant receptors unable to oligomerize can still form dimers (Martínez-Muñoz L. et al. Mol. Cell 2018; García-Cuesta E.M .et al. Proc. Natl. Acad. Sci. USA 2022). Additionally, we believe that these oligomers can also include other chemokine receptors/proteins expressed at the cell membrane, which we are currently studying using different models and techniques.

We have results supporting the existence of CCR5/CXCR4 heterodimers (Martínez-Muñoz L et al. Proc. Natl. Acad. Sci. USA 2014), in line with the data published by Di Marino et al. However, in the current study we have not evaluated the impact of the selected compounds on other CXCR4 complexes distinct from CXCR4 oligomers. Our Jurkat cells do not express CCR5 and, therefore, we cannot discuss whether AGR1.137 affects CCR5/CXCR4 heterodimers. The chemokine field is very complex and most receptors can form dimers (homo- and heterodimers) as well as oligomers (Martinez-Muñoz L., et al Pharmacol & Therap. 2011) when co-expressed. To evaluate different receptor combinations in the same experiment is a complex task, as the number of potential combinations between distinct expressed receptors makes the analysis very difficult. We started with CXCR4 as a model, to continue later with other possible CXCR4 complexes. In addition, for the analysis of CCR5/CXCR4 dynamics, it is much better to use dual-TIRF techniques, which allow the simultaneous detection of two distinct molecules coupled to different fluorochromes.

Regarding the data of Di Marino et al., it is possible that the compounds might also affect heterodimeric conformations of CXCR4. This aspect has also been broached in the revised discussion. We would again note that we evaluated CXCR4 oligomers and not monomers or dimers; this is especially relevant when we compare the residues involved in these processes as they might differ depending on the receptor conformation considered. This issue was also hypothesized by Di Marino et al. (see our response to point 4).

(15) When referring to "unstimulated" cells, provide a more detailed explanation to elucidate the experimental conditions and cellular state under consideration.

Unstimulated cells refer to the cells in basal conditions, that is, cells in the absence of CXCL12. For TIRF-M experiments, transiently-transfected Jurkat cells were plated on glass-bottomed microwell dishes coated with fibronectin; these are the unstimulated cells. To observe the effect of the ligand, dishes were coated as above plus CXCL12 (stimulated cells). We have clarified this point in the material and methods section of the revised version.

(16) 2. Paragraph Organization

-Reorganize the second paragraph to eliminate redundancy and improve overall flow. A more concise and fluid presentation will facilitate reader comprehension and engagement.

The second paragraph has been reorganized to improve overall flow.

(17) Ensure that each paragraph contributes distinct information, avoiding repetition and redundancy.

We have carefully revised each paragraph of the manuscript to avoid redundancy.

(18) 3. Claim of Allosteric Antagonism:

-Exercise caution when asserting that "AGR1.135 and AGR1.137 behave as allosteric antagonists of CXCR4" based on the presented results. Consider rephrasing to reflect that the observed effects suggest the potential allosteric nature of these compounds, acknowledging the need for further investigations and evidence.

To avoid misinterpretations on the effect of the compounds on CXCR4, as we have commented in our response to point 2, we have substituted the term allosteric inhibitors with negative allosteric modulators, which refer to molecules that act by binding a site distinct from the orthosteric site, and selectively block some downstream signaling pathways, whereas others induced by the same endogenous or orthosteric agonist are unaffected (Gao Z.-G. & Jacobson K.A. Drug Discov. Today Technol. 2013). Our data indicate that the selected small compounds do not block ligand binding or G protein activation or receptor internalization, but inhibit receptor oligomerization and ligand-mediated directed cell migration.

(19) In the Results section discussing the "incomplete abolition of CXCR4-mediated responses in Jurkat cells by AGR1.135 and AGR1.137", several points can be refined for better clarity and completeness:  1. Inclusion of Positive Controls: 

-Consider incorporating positive controls in relevant experiments to provide a comparative benchmark for assessing the impact of AGR1.135 and AGR1.137. This addition will strengthen the interpretation of results and enhance the experimental rigor. 

The in vivo experiments (Fig. 7E,F) used AMD3100, an orthosteric antagonist of CXCR4, as a positive control. We also included AMD3100, as a positive control of inhibition when evaluating the effect of the compounds on CXCL12 binding (Fig. 3, new Supplementary Fig. 3). The revised version of the manuscript also includes the effect of this inhibitor on other relevant CXCL12-mediated responses such as cell migration (Fig. 1B), receptor internalization (Fig. 3A), cAMP production (Fig. 3C), ERK1/2 and AKT phosphorylation (Supplementary Fig. 4), actin polymerization (Fig. 4A), cell polarization (Fig. 4B, C) and cell adhesion (Fig. 4D), to facilitate the interpretation of the results and improve the experimental rigor.

(20) 2. Clarification of Terminology: 

-Clarify the term "CXCR4 internalizes" by providing context, perhaps explaining the process of receptor internalization and its relevance to the study.

We refer to CXCR4 internalization as a CXCL12-mediated endocytosis process that results in reduction of CXCR4 levels on the cell surface. We use CXCR4 internalization in this study with two purposes: First, for CXCR4 and other chemokine receptors, internalization processes are mediated by ligand-induced clathrin vesicles (Venkatesan et al 2003) a process that triggers CXCR4 aggregation in these vesicles. We have previously determined that the oligomers of receptors detected by TIRF-M remain unaltered in cells treated with inhibitors of clathrin vesicle formation and of internalization processes (Martinez-Muñoz L. et al. Mol. Cell 2018). Moreover, we have described a mutant CXCR4 that cannot form oligomers but internalizes normally in response to CXCL12 (Martinez-Muñoz L. et al. Mol. Cell 2018). The observation in this manuscript of normal CXCL12-mediated endocytosis in the presence of the negative allosteric inhibitors of CXCR4 that abrogate receptor oligomerization reinforces the idea that the oligomers detected by TIRF are not related to receptor aggregates involved in endocytosis; Second, receptor internalization is not affected by the allosteric compounds, indicating that they downregulate some CXCL12-mediated signaling events but not others (new Fig. 3).

All these data have been included in the revised discussion of the manuscript.

(21) Elaborate on the meaning of "CXCL12 triggers normal CXCR4mut internalization" to enhance reader understanding.

We have previously described a triple-mutant CXCR4 (K239L/V242A/L246A; CXCR4mut). The mutant residues are located in the N-terminal region of TMVI, close to the cytoplasmic region, thus limiting the CXCR4 pocket described in this study (see our response to point 3). This mutant receptor dimerizes but neither oligomerizes in response to CXCL12 nor supports CXCL12-induced directed cell migration, although it can still trigger some Ca2+ flux and is internalized after ligand activation (Martinez-Muñoz L. et al. Mol. Cell 2018).  We use the behavior of this mutant (CXCR4mut) to show that the CXCR4 oligomers and the complexes involved in internalization processes are not the same and to explain why we evaluated CXCR4 endocytosis in the presence of the negative allosteric modulators.

As we indicated in a previous answer to the reviewer, these issues have been re-elaborated in the revised version.

(22) 3. Discrepancy in CXCL12 Concentration:

-Address the apparent discrepancy between the text stating, "...were stimulated with CXCL12 (50 nM, 37{degree sign}C)," and the figure caption (Fig. 3A) reporting a concentration of 12.5 nM. Rectify this inconsistency and provide an accurate and clear explanation.

We apologize for this error, which is now corrected in the revised manuscript. With the exception of the cell migration assays in Transwells, where the optimal concentration was established at 12.5 nM, in the remaining experiments the optimal concentration of CXCL12 employed was 50 nM. These concentrations were optimized in previous works of our laboratory using the same type of experiment. We should also remark that in the experiments using lipid bilayers or TIRF-M experiments, CXCL12 is used to coat the plates and therefore it is difficult to determine the real concentration of the ligand that is retained in the surface of the plates after the washing steps performed prior to adding the cells. In addition, we use 100 nM CXCL12 to create the gradient in the chambers used to perform the directed-cell migration experiments.

(23) 4. Speculation on CXCL12 Binding:

-Refrain from making speculative statements, such as "These data suggest that none of the antagonists alters CXCL12 binding to CXCR4," unless there is concrete evidence presented up to that point. Clearly outline the results that support this conclusion.

Figure 3B and Supplementary Figure 3 show CXCL12-ATTO700 binding by flow cytometry in cells pretreated with the negative allosteric modulators. We have also included AMD3100, the orthosteric antagonist, as a control for inhibition. While these experiments showed no major effect of the compounds on CXCL12 binding, we cannot discard small changes in the affinity of the interaction between CXCL12 and CXCR4. In consequence we have re-written these statements.

(24) 5. Corroboration of Data:

-Specify where the corroborating data from immunostaining and confocal analysis are reported, ensuring readers can access the relevant information to support the conclusions drawn in this section.

In agreement with the suggestion of the reviewer, the revised manuscript includes data from immunostaining and confocal analysis to complement Fig. 4B (new Fig. 4C). The revised version also includes some representative videos for the TIRF experiments showed in Figure 2 to clarify readability.

(25) In the Results section concerning "AGR1.135 and AGR1.137 antagonists and their direct binding to CXCR4", several aspects need clarification and refinement for a more comprehensive and understandable presentation: 1. Workflow Clarification:

-Clearly articulate the workflow used for assessing the binding of AGR1.135 and AGR1.137 to CXCR4. Address the apparent contradiction between the inability to detect a direct interaction and the utilization of Glide for docking in the TMV-TMVI cleft.

To address the direct interaction of the compounds with CXCR4, we intentionally avoided the modification of the small compounds with different labels, which could affect their properties. We therefore attempted a fluorescence a spectroscopy strategy to formally prove the ability of the small compounds to bind CXCR4, but this failed because the AGR1.135 is yellow in color, which interfered with the determinations. We also tried a FRET strategy (see new Supplementary Fig. 7) and detected a significant increase in FRET efficiency of CXCR4 homodimers when AGR1.135 was evaluated, but again the yellow color interfered with FRET determinations. Moreover, AGR1.137 did not modify FRET efficiency of CXCR4 dimers. Therefore, we were unable to detect the interaction of the compounds with CXCR4.

We elected to develop an indirect strategy; in silico, we evaluated the binding-site using docking and molecular dynamics to predict the most promising CXCR4 binding residues involved in the interaction with the selected compounds. Next, we generated point mutant receptors of the predicted residues and re-evaluated the behavior of the allosteric antagonists in a CXCL12-induced cell migration experiment. Obviously, we first discarded those CXCR4 mutants that were not expressed on the cell membrane as well as those that were not functional when activated with CXCL12. Using this strategy, we eliminated the interference due to the physical properties of the compounds and demonstrated that if the antagonism of a compound is reversed in a particular CXCR4 mutant it is because the mutated residue participates or interferes with the interaction between CXCR4 and the compound, thus assuming (albeit indirectly) that the compound binds CXCR4. 

To select the specific mutations included in the analysis, our strategy was to generate point mutations in residues present in the TMV-TMVI pocket of CXCR4 that were not directly proposed as critical residues involved in chemokine engagement, signal initiation, signal propagation, or G protein-binding, based on the extensive mutational study published by Wescott MP et. al. (Wescott M.P. et. al. Proc. Natl. Acad. Sci. U S A. 2016).

(26) Provide a cohesive explanation of the transition from docking evaluation to MD analysis, ensuring a transparent representation of the methodology.

Based on the aim of this work, the workflow shown in Author response image 2, was proposed to predict the binding mode of the selected molecules. Firstly, a CXCR4 model was generated to reconstruct some unresolved parts of the protein structure; then a binding site search using PELE software was performed to identify the most promising binding sites; subsequently, docking studies were performed to refine the binding mode of the molecules; and finally, molecular dynamics simulations were run to determine the most stable poses and predict the residues that we should mutate to test that the compounds interact with CXCR4. 

Author response image 2.

Workflow followed to determine the binding mode of the  studied compounds.

(27) 2. Choice of Software and Techniques:

-Justify the use of "AMBER14" and the PELE approach, considering  their potential obsolescence.

These experiments were performed five years ago when the project was initiated. As the reviewer indicates, AMBER14 and PELE approaches might perhaps be considered obsolescent. Thus, we have predicted the structure of the target using AlphaFold (Jumper J. et al, Nature 2021) and the sequence available under UniProt entry P61073. The complete analysis performed (see our response to point 4) confirmed that the compounds bound the selected pocket, as we had originally determined using PELE. These new analyses have been incorporated into the revised manuscript.

(28)-Discuss the role of the membrane in the receptor-ligand interac7on. Elaborate on how the lipidic double layer may influence the binding of small compounds to GPCRs embedded in the membrane.

Biological membranes are vital components of living organisms, providing a diffusion barrier that separates cells from the extracellular environment, and compartmentalizing specialized organelles within the cell. In order to maintain the diffusion barrier and to keep it electrochemically sealed, a close interaction of membrane proteins with the lipid bilayer is necessary. It is well known that this is important, as many membrane proteins undergo conformational changes that affect their transmembrane regions and that may regulate their activity, as seen with GPCRs (Daemen F.J. & Bonting S.L., Biophys. Struct. Mech. 1977; Gether U. et al. EMBO J. 1997). The lateral and rotational mobility of membrane lipids supports the sealing function while allowing for the structural rearrangement of membrane proteins, as they can adhere to the surface of integral membrane proteins and flexibly adjust to a changing microenvironment. In the case of the first atomistic structure of CXCR4 (Wu B. et al. Science 2010), it was indicated that for dimers, monomers interact only at the extracellular side of helices V and VI, leaving at least a 4-Å gap between the intracellular regions, which is presumably filled by lipids. In particular, they indicated that the channel between TMV and TMVI that connects the orthosteric chemokine binding pocket to the lipid bilayer is occupied by an oleic acid molecule. Recently, Di Marino et al., analyzing the dimeric structure of CXCR4, found a cholesterol molecule placed in between the two protomers, where it engages a series of hydrophobic interactions with residues located in the area between TMI and TMVI (Leu132, Val214, Leu216, Leu246, and Phe249). The polar head of cholesterol forms an H-bond with Tyr135 that further stabilizes its binding mode. This finding confirms that cholesterol might play an important role in mediating and stabilizing receptor dimerization, as seen in other GPCRs (Pluhackova, K., et al. PLoS Comput. Biol. 2016). In addition, we have previously observed that, independently of the structural changes on CXCR4 triggered by lipids, the local lipid environment also regulates CXCR4 organization, dynamics and function at the cell membrane and modulates chemokine-triggered directed cell migration. Prolonged treatment of T cells with bacterial sphingomyelinase promoted the complete and sustained breakdown of sphingomyelins and the accumulation of the corresponding ceramides, which altered both membrane fluidity and CXCR4 nanoclustering and dynamics. Under these conditions, CXCR4 retained some CXCL12-mediated signaling activity but failed to promote efficient directed cell migration (Gardeta S.R. et al. Front. Immunol. 2022). Collectively, these data demonstrate the key role that lipids play in the stabilization of CXCR4 conformations and in regulating its lateral mobility, influencing their associated functions. These considerations have been included in the revised version of the manuscript. 

(29) 3. Stable Trajectories and Binding Mode Superimposi7on -Specify the criteria for defining "stable trajectories" to enhance reader understanding

There could be several ways to describe the stability of a MD simulation, based on the convergence of energies, distances or ligand-target interactions, among others. In this work, we use the expression “stable trajectories” to refer to simulations in which the ligand trajectory converges and the ligand RMSD does not fluctuate more than 0.25Å. This definition is now included in the revised text.

(30)  Clarify the meaning behind superimposing the two small compounds and ensure that the statement in the figure caption aligns with the information presented in the main text.

We apologize for the error in the previous Fig. 5A and in its legend. The figure was created by superimposing the protein component of the poses for the two compounds, AGR1.135 and AGR1.137, rather than the compounds themselves. As panel 5A was confusing, we have modified all Fig. 5 in the revised manuscript to improve clarity.

(31) 4. Volume Analysis and Distances:

-Provide details on how the volume analysis was computed and how distances were accounted for. Consider adding a figure to illustrate these analyses, aiding reader comprehension.

The cleft search and analysis were performed using the default settings of SURFNET (Laskowski R.A. J. Mol. Graph. 1995) included in the PDBsum server (Laskowski R.A. et. al. Trends Biochem. Sci. 1997). The first run of the input model for CXCR4 3ODU identified a promising cleft of 870 Å3 in the lower half of the region flanked by TMV and TMVI, highlighting this area as a possible small molecule binding site (Fig. I, only for review purposes). Analysis of the cleft occupied by AGR1.135 showed two independent cavities of 434 Å3 and 1381 Å3 that were not connected to the orthosteric site. The same procedure for AGR1.137 revealed two distinct clefts of 790 Å3 and 580 Å3, respectively (Fig. I, only for review purposes). Analysis of the atomic distances between the protein residues and the compounds was performed using the PISA server. Krissinel E. & Henrick K. J. Mol. Biol. 2007). (Please see our response to point 3 and the corresponding figure).

(32) 5. Mutant Selection and Relevance:

-Clarify the rationale behind selecting the CXCR4 mutants used in the study. Consider justifying the choice and exploring the possibility of performing an alanine (ALA) scan for a more comprehensive mutational analysis.  

The selection of the residues to be mutated along the cleft was first based on their presence in the proposed cleft and the direct interaction of the compounds with them, either by hydrogen bonding or by hydrophobic interactions. Secondly, all mutated residues did not belong to any of the critical residues involved in transmitting the signal generated by the interaction of CXCL12 with the receptor. In any case, mutants producing a non-functional CXCR4 at the cell membrane were discarded after FACS analysis and chemotaxis experiments. Finally, the length and nature of the resulting mutations were designed mainly to occlude the cleft in case of the introduction of long residues such as lysines (I204K, L208K) or to alter hydrophobic interactions by changing the carbon side chain composition of the residues in the cleft. Indeed, we agree that the alanine scan mutation analysis would have been an alternative strategy to evaluate the residues involved in the interactions of the compounds. 

(33) Reevaluate the statement regarding the relevance of the Y256F muta7on for the binding of AGR1.137. If there is a significant impact on migra7on in the mutant (Fig. 6B), elaborate on the significance in the context of AGR1.137 binding.

In the revised discussion we provide more detail on the relevance of Y256F mutation for the binding of AGR1.137 as well as for the partial effect of G207I and R235L mutations. The predicted interactions for each compound are depicted in new Fig. 6 C, D after LigPlot+ analysis (Laskowski R.A. & Swindells M.B. J. Chem. Inf. Model. 2011), showing that AGR1.135 interacted directly with the receptor through a hydrogen bond with Y256. When this residue was mutated to F, one of the anchor points for the compound was lost, weakening the potential interaction in the region of the upper anchor point.

It is not clear how the Y256F mutation will affect the binding of AGR1.137, but other potential contacts cannot be ruled out since that portion of the compound is identical in both AGR1.135 and AGR1.137. This is especially true for its neighboring residues in the alpha helix, F249, L208, as shown in 3ODU structure (Fig. 6D), which are shown to be directly implicated in the interaction of both compounds. Alternatively, we cannot discard that Y256 interacts with other TMs or lipids stabilizing the overall structure, which could reverse the effect of the mutant at a later stage (Author response image 3).

Author response image 3.

Cartoon representation of Y256 and its intramolecular interactions in the CXCR4 Xray solved structure 3ODU. TMV helix is colored in blue and TMVI in pink.

(34) Address the apparent discrepancy in residue involvement between AGR1.135 and AGR1.137, particularly if they share the same binding mode in the same clef.

AGR1.135 and AGR1.137 exhibit comparable yet distinct binding modes, engaging with CXCR4 within a molecular cavity formed by TMV and TMVI. AGR1.135 binds to CXCR4 through three hydrogen bonds, two on the apical side of the compound that interact with residues TMV-G207 and TMVI-Y256 and one on the basal side that interacts with TMVI-R235 (Fig. 5A). This results in a more extended and rigid conformation when sharing hydrogen bonds, with both TMs occupying a surface area of 400 Å2 and a length of 20 Å in the cleft between TMV and TMVI (Supplementary Fig. 8A). AGR1.137 exhibits a distinct binding profile, interacting with a more internal region of the receptor. This interaction involves the formation of a hydrogen bond with TMIIIV124, which induces a conformational shift in the TMVI helix towards an active conformation (Fig. 5B; Supplementary Fig. 13). Moreover, AGR1.137 may utilize the carboxyl group of V124 in TMIII and overlap with AGR1.135 binding in the cavity, interacting with the other 19 residues dispersed between TMV and VI to create an interaction surface of 370 Å2 along 20 Å (Supplementary Fig. 8B). This is illustrated in the new Fig. 5B. AGR1.137 lacks the phenyl ring present in AGR1.135, resulting in a shorter compound with greater difficulty in reaching the lower part of TMVI where R235 sits. 

Author response image 4.

AGR1.135 and AGR1.137 interaction with TMV and TMVI.  The model shows the location of the compounds within the TMV-VI cleft, illustrated by a ribbon and stick representation. The CXCR4 segments of TMV and TMVI are represented in blue and pink ribbons respectively, and side chains for some of the residues defining the cavity are shown in sticks. AGR1.135 and AGR1.137 are shown in stick representation with carbon in yellow, nitrogen in blue, oxygen in red, and fluorine in green. Hydrogen bonds are indicated by dashed black lines, while hydrophobic interactions are shown in green. The figure reproduces the panels A, B of Fig. 5 in the revised manuscript.

(35) In the Results sec7on regarding "AGR1.137 treatment in a zebrafish xenograf model", the following points can be refined for clarity and completeness: 1. Cell Line Choice for Zebrafish Xenograft Model:

-Explain the rationale behind the choice of HeLa cells for the zebrafish xenograft model when the previous experiments primarily focused on Jurkat cells. Address any specific biological or experimental considerations that influenced this decision.

As far as we know, there are no available models of tumors in zebrafish using Jurkat cells. We looked for a tumoral cell system that expresses CXCR4 and could be transplanted into zebrafish. HeLa cells are derived from a human cervical tumor, express a functional CXCR4, and have been previously used for tumorigenesis analyses in zebrafish (Brown H.K. et al. Expert Opin. Drug Discover. 2017; You Y. et al Front. Pharmacol. 2020). These cells grow in the fish and disseminate through the ventral area and can be used to determine primary tumor growth and metastasis. Nonetheless, we first analyzed in vitro the expression of a functional CXCR4 in these cells (Supplementary Fig. 10A), whether AGR1.137 treatment specifically abrogated CXCL12-mediated direct cell migration (Fig. 7A, B), as whether it affected cell proliferation (Supplementary Fig. 10B). As HeLa cells reproduce the in vitro effects detected for the compounds in Jurkat cells, we used this model in zebrafish. These issues were already discussed in the first version of our manuscript. 

(36) 2. Toxicity Assessment in Zebrafish Embryos: 

-Clarify the basis for stating that AGR1.137 is not toxic to zebrafish embryos. Consider referencing the Zebrafish Embryo Acute Toxicity Test (ZFET) and provide relevant data on lethal concentration (LC50) and non-lethal toxic phenotypes such as pericardial edema, head and tail necrosis, malformation, brain hemorrhage, or yolk sac edema.

Tumor growth and metastasis kinetics within the zebrafish model have been extensively evaluated in many publications (White R. et al. Nat. Rev. Cancer. 2013; Astell K.R. and Sieger D. Cold Spring Harb. Perspect. Med. 2020; Chen X. et al. Front. Cell Dev. Biol. 2021; Weiss JM. Et al. eLife 2022; Lindhal G. et al NPJ Precis. Oncol. 2024). Our previous experience using this model shows that tumors start having a more pronounced proliferation and lower degree of apoptosis from day 4 onwards, but we cannot keep the tumor-baring larvae for that long due to ethical reasons and also because we don’t see much scientific benefit of unnecessarily extending the experiments. Anti-proliferative or pro-apoptotic effects of drugs can still be observed within the three days, even if this is then commonly seen as larger reduction (instead of a smaller growth as it is commonly seen in for example mouse tumor models) compared to controls. Initially we characterized the evolution of implanted tumors in our system and how much they metastasize over time in the absence of treatment before to test the compounds (Author response image 5).

The in vivo experiments were planned to validate efficacious concentrations of the investigated drugs rather than to derive in vivo IC50 or other values, which require testing of multiple doses. We have, however, included an additional concentration to show concentration-dependence and therefore on-target specificity of the drugs in the revised version of the manuscript (data also being elaborated in ongoing experiments). At this stage, we believe that adding the LC50 does not provide interesting new knowledge, and it is standard to only show results from the experimental endpoint (in our case 3 days post implantation). We agree that showing these new data points strengthens the manuscript and facilitates independent evaluation and conclusions to be drawn from the presented data. We have created new graphs where datapoints for each compound dose are shown.  

Author response image 5.

Evolution of the tumors and metastasis along the time in the absence of any treatment. HeLa cells were labeled with 8 µg/mL Fast-DiI™ oil and then implanted in the dorsal perivitelline space of 2-days old zebrafish embryos. Tumors were imaged within 2 hours of implantation and re-imaged each 24 h for three days. Changes in tumor size was evaluated as tumor area at day 1, 2 and 3 divided by tumor area at day 0, and metastasis was evaluated as the number of cells disseminated to the caudal hematopoietic plexus at day 1, 2 and 3 divided by the number of cells at day  3.

Regarding the statement that AGR1.137 was not toxic, this was based on visual inspection of the zebrafish larvae at the end of the experiment, which also revealed a lack of drug-related mortality in these experiments. There are a number of differences in how our experiment was run compared with the standardized ZFET. ZFET evaluates toxicity from 0 hours post-fertilization to 1 or 2 days post-fertilization, whereas here we exposed zebrafish from 2 days post-fertilization to 5 days post-fertilization. The ZFET furthermore requires that the embryos are raised at 26ºC whereas kept the temperature as close as possible to a physiologically relevant temperature for the tumor cells (36ºC). In the ZFET, embryos are incubated in 96-well plates whereas for our studies we required larger wells to be able to manipulate the larvae and avoid well edge-related imaging artefacts, and we therefore used 24-well plates. As such, the ZFET was for various reasons not applicable to our experimental settings. As we were not interested in rigorously determining the LD50 or other toxicity-related measurements, as our focus was instead on efficacy and we found that the targeted dose was tolerated, we did not evaluate multiple doses, including lethal doses of the drug, and are therefore not able to determine an LD50/LC50. We also did not find drug-induced non-lethal toxic phenotypes in this study, and so we cannot elaborate further on such phenotypes other than to simply state that the drug is well tolerated at the given doses. Therefore, the reference to ZFET in the manuscript was eliminated.

(37) If supplementary information is available, consider providing it for a comprehensive understanding of toxicity assessments. 

The effective concentration used in the zebrafish study was derived from the in vitro experiments. That being said, and as elaborated in our response to comment 36, we have added data for one additional dose to show the dose-dependent regulation of tumor growth and metastasis. 

(38) 3. Optimization and Development of AGR1.137: 

-Justify the need for further optimization and development of AGR1.137 if it has a comparable effect to AMD3100. Explain the specific advantages or improvements that AGR1.137 may offer over AMD3100. 

AGR1.137 is highly hydrophobic and is very difficult to handle, particularly in in vivo assays; thus, for the negative allosteric modulators to be used clinically, it would be very important to increase their solubility in water. Contrastingly, AMD3100 is a water-soluble compound. Before using the zebrafish model, we performed several experiments in mice using AGR1.137, but the inhibitory results were highly variable, probably due to its hydrophobicity. We also believe that it would be important to increase the affinity of AGR1.137 for CXCR4, as the use of lower concentrations of the negative allosteric modulator would limit potential in vivo side effects of the drug. On the other hand, we are also evaluating distinct administration alternatives, including encapsulation of the compounds in different vehicles. These alternatives may also require modifications of the compounds. 

AMD3100 is an orthosteric inhibitor and therefore blocks all the signaling cascades triggered by CXCL12. For instance, we observed that AMD3100 treatment blocked CXCL12 binding, cAMP inhibition, calcium flux, cell adhesion and cell migration (Fig. 3, Fig. 4), whereas the effects of AGR1.137 were restricted to CXCL12-mediated directed cell migration. Although AMD3100 was well tolerated by healthy volunteers in a singledose study, it also promoted some mild and reversible events, including white blood cells count elevations and variations of urine calcium just beyond the reported normal range (Hendrix C.W. et al. Antimicrob. Agents Chemother. 2000). To treat viral infections, continuous daily dosing requirements of AMD3100 were impractical due to severe side effects including cardiac arrhythmias (De Clercq E. Front Immunol. 2015). For AMD3100 to be used clinically, it would be critical to control the timing of administration. In addition, side effects after long-term administration have potential problems. Shorter-term usage and lower doses would be fundamental keys to its success in clinical use (Liu T.Y. et al. Exp. Hematol. Oncol. 2016). The use of a negative allosteric modulator that block cell migration but do not affect other signaling pathways triggered by CXCL12 would be, at least in theory, more specific and produce less side effects. These ideas have been incorporated into the revised discussion to reflect potential advantages or improvements that AGR1.137 may offer over AMD3100.

(39) 4. Discrepancy in AGR1.137 and AMD3100 Effects:

-Discuss the observed discrepancy where AGR1.137 exhibits similar effects to AMD3100 but only after 48 hours. Provide insights into the temporal dynamics of their actions and potential implications for the experimental design.

Images and data shown in Fig. 7E, F correspond to days 0 and 3 after HeLa cell implantation (tumorigenesis) and only to day 3 in the case of metastasis data. The revised version contains the effect of two distinct doses of the compounds (10 and 50 µM, for AGR1.135 and AGR1.137 and 1 and 10 µM for AMD3100). 

(40) In the "Discussion" section, there are several points that require clarifica7on and refinement to enhance the overall coherence and depth of the analysis:  1. Reduction of Side-Effects: 

-Provide a more detailed explanation of how the identified compounds, specifically AGR1.135 and AGR1.137, contribute to the reduction of side effects. Consider discussing specific mechanisms or characteristics that differentiate these compounds from existing antagonists.

The sentence indicating that AGR1.135 and AGR1.137 contribute to reduce side effects is entirely speculative, as we have no experimental evidence to support it. We have therefore corrected this in the revised version. The origin of the sentence was that orthosteric antagonists typically bind to the same site as the endogenous ligand, thus blocking its interaction with the receptor. Therefore, orthosteric inhibitors (i.e. AMD3100) block all signaling cascades triggered by the ligand and therefore their functional consequences. However, the compounds described in this project are essentially negative allosteric modulators, that is, they bind to a site distinct from the orthosteric site, inducing a conformational change in the receptor that does not alter the binding of the endogenous ligand, and therefore block some specific receptor-associated functions without altering others. We observed that AGR1.137 blocked receptor oligomerization and directed cell migration whereas CXCL12 still bound CXCR4, triggered calcium mobilization, did not inhibit cAMP release or promoted receptor internalization. This is why we speculated on the limitation of side effects. The statements have been nonetheless revised in the new version of the manuscript.

(41) 2. Binding Site Clarification:

-Address the apparent discrepancy between docking the small compounds in a narrow cleft formed by TMV and TMVI helices and the statement that AGR1.131 binds elsewhere. Clarify the rationale behind this assertion

After the in silico screening, a total of 40 compounds were selected.  These compounds showed distinct degrees of interaction with the cleft formed by TMV and TMVI and even with other potential interaction sites on CXCR4, with the exception of the ligand binding site according to the data described by Wescott et al. (PNAS 2016 113:9928-9933), as this possibility was discarded in the initial approach of the in silico screening. According to PELE analysis, AGR1.131 was one of the 40 selected compounds that showed a pose with low binding energy, -39.8 kcal/mol, between TMV and TMVI helices, that is, it might interact with CXCR4 through the selected area for the screening. It nonetheless also showed a best pose placed between helices TMI and TMVII, -43.7 kcal/mol. In any case, the compound was included in the biological screening, where it was unable to impact CXCL12-mediated chemotaxis (Fig. 1B). We then focused on AGR1.135 and AGR1.137, as showed a higher inhibitory effect on CXCL12-mediated migration, and on AGR1.131 as an internal negative control. AGR1.131 has a skeleton very similar to the other compounds (Fig. 1C) and can interact with the TM domains of CXCR4 without promoting effects. None of the three compounds affected CXCL12 binding, or CXCL12mediated inhibition of cAMP release, or receptor internalization. However, whereas AGR1.135 and AGR1.137, blocked CXCL12-mediated CXCR4 oligomerization and directed cell migration towards CXCL12 gradients, AGR1.131 had no effect in these experiments (Fig. 3, Fig.  4). 

Next, we performed additional theoretical calculations (PELE, docking, MD) to inspect in detail the potential binding modes of active and inactive molecules. Based on these additional calculations, we identified that whereas AGR1.135 and AGR1.137 showed preferent binding on the molecular pocket between TMV and TMVI, the best pose for AGR1.131 was located between TMI and TMVII, as the initial experiments indicated.  These observations and data have been clarified in the revised discussion. 

(42) 3. Impact of Chemical Modifications:

-Discuss the consequences of the distinct chemical groups in AGR1.135, AGR1.137, and AGR1.131, specifically addressing how variations in amine length and chemical nature may influence binding affinity and biological activity. Provide insights into the potential effects of these modifications on cellular responses and the observed outcomes in zebrafish. 

The main difference between AGR1.131 and the other two compounds is the higher flexibility of AGR1.131 due to the additional CH2 linker, together with the lack of a piperazine ring. The additional CH2 linking the phenyl ring increases the flexibility of AGR1.131 when compared with AGR1.135 and AGR1.137, and the absence of the piperazine ring might be responsible for its lack of activity, as it makes this compound able to bind to CXCR4 (Fig. 1C).

AGR1.137 was chosen in a second round. The additional presence of the tertiary amine (in the piperazine ring) allows the formation of quaternary ammonium salts in the aqueous medium and its substituents to increase its solubility (Fig 1C). This characteristic might be related to the absence of toxic effects of the compound in the zebrafish model.

(43) 4. Existence of Distinct CXCR4 Conformational States: 

-Provide more detailed support for the statement suggesting the "existence of distinct CXCR4 conformational states" responsible for activating different signaling pathways. Consider referencing relevant studies or experiments that support this claim.

Classical models of GPCR allostery and activation, which describe an equilibrium between a single inactive and a single signaling-competent active conformation, cannot account for the complex pharmacology of these receptors. The emerging view is that GPCRs are highly dynamic proteins, and ligands with varying pharmacological properties differentially modulate the balance between multiple conformations.

Just as a single photograph from one angle cannot capture all aspects of an object in movement, no one biophysical method can visualize all aspects of GPCR activation. In general, there is a tradeoff between high-resolution information on the entire protein versus dynamic information on limited regions. In the former category, crystal and cryo-electron microscopy (cryoEM) structures have provided comprehensive, atomic-resolution snapshots of scores of GPCRs both in inactive and active conformations, revealing conserved conformational changes associated with activation. However, different GPCRs vary considerably in the magnitude and nature of the conformational changes in the orthosteric ligand-binding site following agonist binding (Venkatakrishnan A.J.V. et al. Nature 2016). Spectroscopic and computational approaches provide complementary information, highlighting the role of conformational dynamics in GPCR activation (Latorraca N.R.V. et al. Chem. Rev 2017). In the absence of agonists, the receptor population is typically dominated by conformations closely related to those observed in inactive-state crystal structures (Manglik A. et al. Cell 2015). While agonist binding drives the receptor population towards conformations similar to those in activestate structures, a mixture of inactive and active conformations remains, reflecting “loose” or incomplete allosteric coupling between the orthosteric and transducer pockets (Dror R.O. et al. Proc. Natl. Acad. Sci. USA 2011). Surprisingly, for some GPCRs, and under some experimental conditions, a substantial fraction of unliganded receptors already reside in an active-like conformation, which may be related to their level of basal or constitutive signaling (Staus D.P. et al. J. Biol. Chem. 2019);  Ye L. et al. Nature 2016).  In our case, the negative allosteric modulators, (Staus DP, et al. J. Biol. Chem 2019); Ye L. et al. Nature 2016) did not alter ligand binding and had only minor effects on specific CXCL12-mediated functions such as inhibition of cAMP release or receptor internalization, among others, but failed to regulate CXCL12-mediated actin dynamics and receptor oligomerization. Collectively, these data suggest that the described compounds alter the active conformation of CXCR4 and therefore support the presence of distinct receptor conformations that explain a partial activation of the signaling cascade.

All these observations are now included in the revised discussion of the manuscript.

(44) 5. Equilibrium Shift and Allosteric Ligands: 

-Clarify the statement about "allosteric ligands shifting the equilibrium to favor a particular receptor conformation". Support this suggestion with references or experimental evidence

In a previous answer (see our response to point 2), we explain why we define the compounds as negative allosteric modulators. These compounds do not bind the orthosteric binding site or a site distinct from the orthosteric site that alters the ligand-binding site. Their effect should be due to changes in the active conformation of CXCR4, which allow some signaling events whereas others are blocked. Our functional data thus support that through the same receptor the compounds separate distinct receptor-mediated signaling cascades, that is, our data suggest that CXCR4 has a conformational heterogeneity. It is known that GPCRs exhibit more than one “inactive” and “active” conformation, and the endogenous agonists stabilize a mixture of multiple conformations. Biased ligands or allosteric modulators can achieve their distinctive signaling profiles by modulating this distribution of receptor conformations. (Wingler L.M. & Lefkowitz R.J. Trends Cell Biol. 2020). For instance, some analogs of angiotensin II do not appreciably activate Gq signaling (e.g., increases in IP3 and Ca2+) but still induce receptor phosphorylation, internalization, and mitogen-activated protein kinase (MAPK) signaling (Wei H, et al. Proc. Natl. Acad. Sci. USA 2003). Some of these ligands activate Gi and G12 in bioluminescence resonance energy transfer (BRET) experiments (Namkung Y. et al. Sci. Signal. 2018). A similar observation was described in the case of CCR5, where some chemokine analogs promoted G protein subtype-specific signaling bias (Lorenzen E. et al. Sci. Signal 2018). Structural analysis of distinct GPCRs in the presence of different ligands vary considerably in the magnitude and nature of the conformational changes in the orthosteric ligand-binding site following agonist binding (Venkatakrishnan A.J.V. et al. Nature 2016). Yet, these changes modify conserved motifs in the interior of the receptor core and induce common conformational changes in the intracellular site involved in signal transduction. That is, these modifications might be considered distinct receptor conformations. 

The revised discussion contains some of these interpretations to support our statement about the stabilization of a particular receptor conformation triggered by the negative allosteric modulators. 

(45) 6. Refinement of Binding Mode: 

-Clarify the workflow for obtaining the binding mode, particularly the role of GLIDE and PELE. Clearly explain how these software tools were used in tandem to refine the binding mode. 

The computational sequential workflow applied in this project included, i) Protein model construction, ii) Virtual screening (Glide), iii) PELE, iv) Docking (AutoDock and Glide) and v) Molecular Dynamics (AMBER).

Glide was applied for the structure-based virtual screening to explore which compounds could fit and interact with the previously selected binding site.

After the identification of theoretically active compounds (modulators of CXCR4), additional calculations were done to identify a potential binding site. PELE was used in this sense, to study how the compounds could bind in the whole surface of the target (TMV-TMVI). By applying PELE, we avoided biasing the calculation, and we found that the trajectories with better interaction energies identified the cleft between TMV and TMVI as the binding site for AGR1.135 and AGR1.137, and not for AGR1.131. AGR1.131 showed a pose with low binding energy, -39.8 kcal/mol, between TMV and TMVI helices, that is, it might interact with CXCR4 in the selected area for the screening. But it also showed a better pose placed between helices TMI and TMVII, - 43.7 kcal/mol (see our response to point 41). These data have been now confirmed using Schrodinger’s MM-GBSA procedure (see our response to points 6 and 8). In any case, the compound was included in the biological screening, where it was unable to affect CXCL12-mediated chemotaxis (Fig. 1B). Docking and MD simulations were then performed to study and refine the specific binding mode in this cavity. These data were important to choose the mutations on CXCR4 required, to test whether the compounds reversed its behavior. In these experiments we also confirmed that AGR1.131 had a better pose on the TMI-TMVII region. 

(46) 7. Impact of Compound Differences on CXCR4-F249L mutant: 

-Provide visual aids, such as figures, and additional experiments to support the statement about differences in the behavior of AGR1.135 and AGR1.137 on cells expressing CXCR4-F249L mutant. Elaborate on the closer interaction suggested between the triazole group of AGR1.137 and the F249 residue

At the reviewer’s suggestion, Fig. 5 has been modified to incorporate a closer view of the interactions identified and new panels in new Fig. 6 have been added to show in detail the effect of the mutations selected on the structure of the cleft between TMV and TMVI. The main difference between AGR1.135 and AGR1.137 is how the triazole group interacts with F249 and L216 (Author response image 6). In AGR1.137, the three groups are aligned in a parallel organization, which appears to be more effective: This might be due to a better adaptation of this compound to the cleft since there is only one hydrogen bond with V124. In AGR1.135, the compound interacts with the phenyl ring of F249 and has a stronger interaction at the apical edge to stabilize its position in the cleft. However, there is still an additional interaction present. When changing F249

Author response image 6.

Cartoon representation of the interaction of CXCR4 F249L mutant with AGR1.135 (A) and AGR1.137 (B). The two most probable conformations of Leucine rotamers are represented in cyan A and B conformations. Van der Waals interactions are depicted in blue cyan dashed lines, hydrogen bonds in black dashed lines. CXCR4 segments of TMV and TMVI are colored in blue and pink, respectively

to L (Fig. VIIA, B, only for review purposes) and showing the two most likely rotamers resulting from the mutation, it is observed that rotamer B is in close proximity to the compound, which may cause the binding to either displace or adopt an alternative conformation that is easier to bind into the cleft. As previously mentioned, it is likely that AGR1.135 can displace the mutant rotamer and bind into the cleft more easily due to its higher affinity.

(47) In the "Materials and Methods" section, the computational approach for the "discovery of CXCR4 modulators" requires significant revision and clarification. The following suggestions aim to address the identified issues: 1. Structural Modeling: 

-Reconsider the use of SWISS-MODEL if there is an available PDB code for the entire CXCR4 structure. Clearly articulate the rationale for choosing one method over the other and explain any limitations associated with the selected approach. 

The SWISS-model server allows for automated comparative modeling of 3D protein structures that was pioneered in the fields of automated modeling. At the time we started this project. it was the most accurate method to generate reliable 3D protein structure models.

As explained above, we have now predicted the structure of the target using AlphaFold (Jumper J. et al, Nature 2021) and performed several additional experiments that confirm that the small compounds bind the selected pocket as the original strategy indicated (see our response to point 6). (Fig. II, only for review purposes).

(48) 2. Parametriza7on of Small Compounds: 

-Provide a detailed description of the parametrization process for the small compounds used in the study. Specify the force field and parameters employed, considering the obsolescence of AMBER14 and ff14SB. Consider adopting more contemporary force fields and parameterization strategies. 

When we performed these experiments, some years ago, the force fields applied (ff14SB, AMBER14 used in MD or OPLS2004 in docking with Glide) were well accepted and were gold standards. It is, however, true that the force fields have evolved in the past few years, Moreover, in the case of the MD simulations, to consider the parameters of the ligands that are not contained within the force field, we performed an additional parameterization as a standard methodology. We then generated an Ab initio optimization of the ligand geometry, defining as basis sets B3LYP 6-311+g(d), using Gaussian 09, Revision A.02, and then a single point energy calculation of ESP charges, with HF 6311+g(d) on the optimized structure. As the last step of the parametrization, the antechamber module was used to adapt these charges and additional parameters for MD simulations.

(49) 3. Treatment of Lipids and Membrane: 

-Elaborate on how lipids were treated in the system. Clearly describe whether a membrane was included in the simulations and provide details on its composition and structure. Address the role of the membrane in the study and its relevance to the interactions between CXCR4 and small compounds 

To stabilize CXCR4 and more accurately reproduce the real environment in the MD simulation, the system was embedded in a lipid bilayer using the Membrane Builder tool (Sunhwan J. et al. Biophys. J. 2009) from the CHARMM-GUI server. The membrane was composed of 175 molecules of the fatty acid 1-palmitoyl-2-oleoyl-sn-glycero-3phosphocholine (POPC) in each leaflet. The protein-membrane complex was solvated with TIP3 water molecules. Chloride ions were added up to a concentration of 0.15 M in water, and sodium ions were added to neutralize the system. This information was previously described in detail.

(50) 4. Molecular Dynamics Protocol: 

-Provide a more detailed and coherent explanation of the molecular dynamics protocol. Clarify the specific steps, parameters, and conditions used in the simulations. Ensure that the protocol aligns with established best practices in the field.

Simulations were calculated on an Asus 1151 h170 LVX-GTX-980Ti workstation, with an Intel Core i7-6500 K Processor (12 M Cache, 3.40 GHz) and 16 GB DDR4 2133 MHz RAM, equipped with a Nvidia GeForce GTX 980Ti available for GPU (Graphics Processing Unit) computations. MD simulations were performed using AMBER14 (Case D.A. et al. AMBERT 14, Univ. of California, San Francisco, USA, 2014) with ff14SB (Maier J.A. et al. J. Chem. Theory Comput. 2015) and lipid14 (Dickson C. J. et al. J. Chem. Theory Comput. 2014) force fields in the NPT thermodynamic ensemble (constant pressure and temperature). Minimization was performed using 3500 Steepest Descent steps and 4500 Conjugate Gradient steps three times, firstly considering only hydrogens, next considering only water molecules and ions, and finally minimizing all atoms. Equilibration raises system temperature from 0 to 300 K at a constant volume fixing everything but ions and water molecules. After thermalization, several density equilibration phases were performed. In the production phase, 50 ns MD simulations without position restraints were calculated using a time step of 2 fs. Trajectories of the most interesting poses were extended to 150 ns. All bonds involving hydrogen atoms were constrained with the SHAKE algorithm (Lippert R.A. et al. J. Chem. Phys. 2007). A cutoff of 8 Å was used for the Lennard-Jones interaction and the short-range electrostatic interactions. Berendsen barostat (Berendsen H.J. et al. J. Chem. Phys.  1984) and Langevin thermostat were used to regulate the system pression and temperature, respectively. All trajectories were processed using CPPTRAJ (Roe D.R. & Cheatham III T.E. J. Chem. Theory Comput. 2013) and visualized with VMD (Visual Molecular Dynamics) (Humphrey W. et al. J. Mol. Graphics. 1996). To reduce the complexity of the data, Principal Component Analysis (PCA) was performed on the trajectories using CPPTRAJ.

(51) Consider updating the molecular dynamics protocol to incorporate more contemporary methodologies, considering advancements in simulation techniques and software.

In our answer to points 6 and 47, we describe why we use the technology based on Swiss-model and PELE analysis and how we have now used Alphafold and other more contemporary methodologies to confirm that the small compounds bind the selected pocket.

(52) Figure 1A: 

•  Consider switching to a cavity representation for CXCL12 to enhance clarity and emphasize the cleft.

Fig. 1A has been modified to emphasize the cleft.

(53) Explicitly show the TMV-TMVI cleft in the figure for a more comprehensive visualization. 

In Fig. 1A we have added an insert to facilitate TMV-TMVI visualization.

(54) Figure 1B: 

•  Clearly explain the meaning of the second DMSO barplot to avoid confusion. 

To clarify this panel, we have modified the figure and the figure legend. Panel B now includes a complete titration of the three compounds analyzed in the manuscript.  The first bar shows cell migration in the absence of both treatment with AMD3100 and stimulation with CXCL12.  The second bar shows migration in response to CXCL12 in the absence of AMD3100. The third bar shows the effect of AMD3100 on CXCL12-induced migration, as a known control of inhibition of migration.  We hope that this new representation of the data results is clearer.

(55) Figure 1C: 

•  Provide a clear legend explaining the significance of the green shading on the small compounds. 

The legend for Fig. 1C has been modified accordingly to the reviewer’s suggestion.

(56) Figure 2: 

•  Elaborate on the role of fibronectin in the experiment and explain the specific contribution of CD86-AcGFP.

The ideal situation for TIRF-M determinations is to employ cells on a physiological substrate complemented with or without chemokines. Fibronectin is a substrate widely used in different studies that allows cell adhesion, mimicking a physiological situation. Jurkat cells express alpha4beta1 and alpha5beta1 integrins that mediate adhesion to fibronectin (Seminario M.C. et al. J. Leuk. Biol. 1999).

Regarding the use of CD86-AcGFP in TIRF-M experiments. We currently determine the number of receptors in individual trajectories of CXCR4 using, as a reference, the MSI value of CD86-AcGFP that strictly showed a single photobleaching step (Dorsch S. et al. Nat Methods 2009).

We preferred to use CD86-AcGFP in cells instead of AcGFP on glass, to exclude any potential effect on the different photodynamics exhibited by AcGFP when bound directly to glass. In any case, this issue has been clarified in the revised version.

(57) Figure 3D: 

•  Include a plot for the respective band intensity to enhance data presentation 

The plot showing the band intensity analysis of the experiments shown in Fig. 3D was already included in the original version (see old Supplementary Fig. 3). However, in the revised version, we include these plots in the same figure as panels 3E and 3F.  As a control of inhibition of CXCL12 stimulation, we have also included a new figure (Supplementary Fig. 4) showing the effect of AMD3100 on CXCL12-induced activation of Akt and ERK as analyzed by western blot.

(58) Consider adding AMD3100 as a control for comparison. 

In agreement with the reviewer’s suggestion, we have added the effect of AMD3100 in most of the functional experiments performed.

(59) Figure 4: 

•  Address the lack of positive controls in Figure 4 and consider their inclusion for a more comprehensive analysis. 

DMSO bars correspond to the control of the experiment, as they represent the effect of CXCL12 in the absence of any allosteric modulator. As previously described in this point-by-point reply, DMSO bars correspond to the control performed with the solvent with which the small compounds, at maximum concentration, are diluted.  Therefore, they show the effect of the solvent on CXCL12 responses. In any case, and in order to facilitate the comprehension of the figure we have also added the controls in the absence of DMSO to demonstrate that the solvent does not affect CXCL12-mediated functions, together with the effect of the orthosteric inhibitor AMD3100. In addition, we have also included representative images of the effect of the different compounds on CXCL12-induced polarization (Fig. 4C).

(60) In Figure 4A, carefully assess overlapping error bars and ensure accurate interpreta7on. If necessary, consider alternative representation. 

We have tried alternative representations of data in Fig. 4A, but in all cases the figure was unclear. We believe that the way we represent the data in the original manuscript is the most clear and appropriate.  Nevertheless, we have now included significance values as a table annexed to the figure, as well as the effect of AMD3100, as a control of inhibition

(61) Supplementary Figure 1A: 

•  Improve the clarity of bar plots for better understanding. Consider reordering them from the most significant to the least. 

This was a good idea, and therefore Supplementary Fig. 1A has been reorganized to improve clarity.

(62) Supplementary Figure 1C: 

•  Clarify the rationale behind choosing the 12.5 nM concentration and explain if different concentrations of CXCL12 were tested. 

In old Supplementary Fig. 1C, we used untreated cells, that is, CXCL12 was not present in the assay.  These experiments were performed to test the potential toxicity of DMSO (solvent) or the negative allosteric modulators on Jurkat cells. The 12.5 nM concentration of CXCL12 mentioned in the figure legend applied only to panels A and B, as indicated in the figure legend. We previously optimized this concentration for Jurkat cells using different concentrations of CXCL12 between 5 and 100 nM.  Nevertheless, we have reorganized old supplementary fig. 1 and clarified the figure legend to avoid misinterpretations (see Supplementary Fig 1A, B and Supplementary Fig. 2A, B).

(63) Explain the observed reduction in fluorescence intensity for AGR1.135. 

The cell cycle analysis has been moved from Supplementary Fig. 1C to a new Supplementary Fig. 2.  It now includes the flow cytometry panels to show fluorescence intensity as a function of the number of cells analyzed (Panel 1A) as well as a table (panel B) with the percentage of cells in each phase of the cell cycle. We believe that the apparent reduction in fluorescence that the reviewer observes is mainly due to the number of events analyzed. However, we have changed the flow cytometry panels for others that are more representative and included a table with the mean of the different results. When we determined the percentage of cells in each cell cycle phase, we observed that it looks very similar in all the experimental conditions. That is, none of the compounds affected any of the cell cycle phases. We have also included the effect of H2O2 and staurosporine as control compounds inducing cell death and cell cycle alteration of Jurkat cells.

(64) Supplementary Table 1: 

•  Include a column specifying the scoring for each compound to provide a clear reference for readers. 

To facilitate references to readers, we have now included the inhibitory effect of each compound on Jurkat cell migration in the revised version of this table. 

(65) Minor Points 

Page 2 - Abstract: Rephrase the first sentence of the abstract to enhance fluidity. 

Although the entire manuscript was revised by a professional English editor, we appreciate the valuable comments of this reviewer and we have corrected these issues accordingly.

(66) Page 2 - Abstract: Explicitly define "CXCR4" as "C-X-C chemokine receptor type 4" the first time it appears.

We have not used C-X-C chemokine receptor type 4 the first time it appears in the abstract. CXCR4 is an acronym normally accepted to identify this chemokine receptor, and it is used as CXCR4 in many articles published in eLife. However, we introduce the complete name the first time it appears in the introduction.

(67) Page 2 - Abstract: Explicitly define "CXCL12" as "C-X-C motif chemokine 12" the first time it is mentioned. 

As we have discussed in the previous response, we have not used C-X-C motif chemokine 12 the first time CXCL12 appears in the abstract, as it is a general acronym normally accepted to identify this specific chemokine, even in eLife papers. However, we introduce the complete name the first time it appears in the introduction section.

(68) Page 2 - Abstract: Explicitly define "TMV and TMVI" upon its first mention.

The acronym TM has been defined as “Transmembrane” in the revised version

(69) Page 2 - Abstract: Review the use of "in silico" in the sentence for accuracy and consider revising if necessary.

With the term “in silico” we want to refer to those experiments performed on a computer or via computer simulation software. We have carefully reviewed its use in the new version of the manuscript.

(70) Page 2 - Abstract: Add a comma after "compound" in the sentence, "We identified AGR1.137, a small compound that abolishes...".

A comma after “compound” has been added in the revised sentence.

(71) Page 2 - Significance Statement: Rephrase the first sentence of the "Significance Statement" to avoid duplication with the abstract.

The first sentence of the Significance Statement has been revised to avoid duplication with the abstract. 

(72) Page 2 - Significance Statement: Break down the lengthy sentence, "Here, we performed in silico analyses..." for better readability. 

The sentence starting by “Here, we performed in silico analyses…” has been broken down in the revised manuscript.

(73) Page 2 - Introduction: Replace "Murine studies" with a more specific term for clarity.

The term “murine studies” is normally used to refer to experimental studies developed in mice. We have nonetheless rephrased the sentence.

(74) Page 3 - Introduction: Rephrase the sentence for clarity: "Finally, using a zebrafish model, ..."

The sentence has been now rephrased for clarity.

(75) Results-AGR1.135 and AGR1.137 block CXCL12-mediated CXCR4 nanoclustering and dynamics: 

Rephrase the sentence for clarity: "Retreatment with AGR1.135 and AGR1.137, but not with AGR1.131, substantially impaired CXCL12-mediated receptor nanoclustering.”

The sentence has been rephrased for clarity.

(76) Results - AGR1.135 and AGR1.137 incompletely abolish CXCR4-mediated responses in Jurkat cells: Clarify the sentence: "In contrast to the effect promoted by AMD3100, a binding-site antagonist of CXCR4..."

The sentence has been modified for clarity.

(77) Consider using "orthosteric" instead of "binding-site" antagonist.

The term orthosteric is now used throughout to refer to a binding site antagonist.

(78) Discussion: Use the term "in silico" only when necessary.

We have carefully reviewed the use of “in silico” in the manuscript.

(79) Discussion: Clarify the sentence: "...not affect neither CXCR2-mediated cell migration...". Confirm if "CXCL12" is intended.

The sentence refers to the chemokine receptor CXCR2, which binds the chemokine CXCL2. To test the specificity of the compounds for the CXCL12/CXCR4 axis, we evaluated CXCL2-mediated cell migration.  The results indicated that CXCL2/CXCR2 axis was not affected by the negative allosteric modulators, whereas CXCL12-mediated cell migration was blocked.  The sentence has been clarified in the new version of the manuscript.

(80) Figure 4B: Bold the "B" in the figure label for consistency.

The “B” in Fig. 4B has been bolded.

Reviewer #2

(1) Fig 2. The SPT data is sub-optimal in its presentation as well as analysis. Example images should be shown. The analysis and visualization of the data should be reconsidered for improvements. Graphs with several hundreds, in some conditions over 1000 tracks, per condition are very hard to compare. The same (randomly selected representative set) number of data points should be shown for better visualization. Also, more thorough analyses like MSD or autocorrelation functions are lacking - they would allow enhanced overall representation of the data.

In agreement with the reviewer’s commentary, we have modified the representation of Fig. 2. We have carefully read the paper published by Lord S.J. and col. (Lord S. J. et al., J. Cell Biol. 2020) and we apply their recommendations for these type of data. We have also included as supplementary material representative videos for the TIRF-M experiments performed to allow readers to visualize the original images. Regarding the MSD analyses, they were developed to determine all D1-4 values. According to the data published by Manzo & García-Parajo (Manzo C. & García-Parajo M.F. Rep.Prog. Phys. 2015) due to the finite trajectory length the MSD curve at large tlag has poor statistics and deviates from linearity. However, the estimation of the Diffusion Coefficient (D1-4) can be obtained by fitting of the short tlag region of the MSD plot giving a more accurate idea of the behavior of particles. In agreement we show D1-4 values and not MSD data. 

Due to the space restrictions, it is very difficult to include all the figures generated, but, only for review purposes, we included in this point-by-point reply some representative plots of the MSD values as a function of the time from individual trajectories showing different types of motion obtained in our experiments (Author response image 7).

Author response image 7.

Representative MSD plots from individual trajectories of CXCR4-AcGFP showing different types of motion: A) confined, B) Brownian/Free, C) direct transport of CXCR4-AcGFP particles diffusing at the cell membrane detected by SPT-TIRF in resting JKCD4 cells.

Further analysis, such as the classification based on particle motion, has not been included in this article. This classification uses the moment scaling spectrum (MSS), described by Ewers H. et al. 2005 PNAS, and requires particles with longer trajectories (>50 frames). Only for review purposes, we include a figure showing the percentage of the MSS-based particle motion classification for each condition. As expected, most of long particles are confined, with a slight increase in the percentage upon CXCL12 stimulation in all conditions, except in cell treated with AGR1.137 (Author response image 8).

Author response image 8.

Effects of the negative allosteric modulators on the Types of Motion of CXCR4. Percentage of single trajectories with different types of motion, classified by MSS (DMSO: 58 particles in 59 cells on FN; 314 in 63 cells on FN+CXCL12; AGR1.131: 102 particles in 71 cells on FN; 258in 69 cells on FN+CXCL12; AGR1.135: 86 particles in 70 cells on FN; 120 in 77 cells on FN+CXCL12; AGR1.137: 47 particles in 66 cells on FN; 74 in 64 cells on FN+CXCL12) n = 3.

(2) Fig 3. The figure legends have inadequate information on concentrations and incubation times used, both for the compounds and other treatments like CXCL12 and forskolin. For the Western blot data, also the quantification should be added to the main figure. The compounds, particularly AGR1.137 seem to lead to augmented stimulation of pAKT and pERK. This should be discussed

The Fig. 3 legend has been corrected in the revised manuscript. Fig. 3D now contains representative western blots and the densitometry evaluation of these experiments. As the reviewer indicates, we also detected in the western blot included, augmented stimulation of pAKT and pERK in cells treated with AGR1.137. However, as shown in the densitometry analysis, no significant differences were noted between the data obtained with each compound. As a control of inhibition of CXCL12 stimulation we have included a new Supplementary Fig. 4 showing the effect of AMD3100 on CXCL12-induced activation of Akt and ERK as analyzed by western blot.

(3) Fig. 4 immunofluorescence data on polarization as well as the flow chamber data lack the representative images of the data. The information on the source of the T cells is missing. Not clear if this experiment was done on bilayers or on static surfaces.

Representative images for the data shown in Figure 4B have been added in the revised figure (Fig. 4C). The experiments in Fig. 4B were performed on static surfaces. As indicated in the material and methods section, primary T cell blasts were added to fibronectin-coated glass slides and then were stimulated or not with CXCL12 (5 min at 37ºC) prior to fix permeabilize and stain them with Phalloidin. Primary T cell blasts were generated from PBMCs isolated from buffy coats that were activated in vitro with IL-2 and PHA as indicated in the material and methods section.

(4) The data largely lacks titration of different concentrations of the compounds. How were the effective concentration and treatment times determined? What happens at higher concentrations? It is important to show, for instance, if the CXCR12 binding gets inhibited at higher concentrations. most experiments were performed with 50 uM, but HeLa cell data with 100 uM. Why and how was this determined? 

The revised version contains a new panel in Fig. 1B to show a more detailed kinetic analysis with different concentrations (1-100 µM) of the compounds in the migration experiments using Jurkat cells. We choose 50 µM for further studies as it was the concentration that inhibits 50-75% of the ligand induced cell migration. 

We have also included the effect of two doses of the compounds (10 and 50 µM) in the zebrafish model as well as AMD3100 (1 and 10 µM) as control (new Fig. 7D, E).  Tumors were imaged within 2 hours of implantation and tumor-baring embryos were treated with either vehicle (DMSO) alone, AGR1.131 or AGR1.137 at 10 and 50 µM or AMD3100 at 1 and 10 µM for three days, followed by re-imaging.

Regarding the amount of CXCL12 used in these experiments, with the exception of cell migration assays in Transwells, where the optimal concentration was established at 12.5 nM, in all the other experiments the optimal concentration of CXCL12 employed was 50 nM. In the case of the directional cell migration assays, we use 100 nM to create the chemokine gradient in the device. These concentrations have been optimized in previous works of our laboratory using these types of experiments. It should also be noted that in the experiments using lipid bilayers or TIRF-M experiments, CXCL12 is used to coat the plates and therefore it is difficult to determine the real concentration that is retained in the surface after the washing steps performed prior adding the cells.

(5) The authors state that they could not detect direct binding of the compounds and the CXCR14. It should be reported what approaches were tried and discussed why this was not possible. 

We attempted a fluorescence spectroscopy strategy to formally prove the ability of AGR1.135 to bind CXCR4, but this strategy failed because the compound has a yellow color that interfered with the determinations. We also tried a FRET strategy (see supplementary Fig. 7) and detected a significant increase in FRET efficiency of CXCR4 homodimers in cells treated with AGR1.135; this effect was due to the yellow color of this compound that interferes with FRET determinations. In the same assays, AGR1.137 did not modify FRET efficiency for CXCR4 homodimers and therefore we cannot assume that AGR1.137 binds on CXCR4. All these data have been considered in the revised discussion.

(6) The proliferation data in Supplementary Figure 1 lacks controls that affect proliferation and indication of different cell cycle stages. What is the conclusion of this data? More information on the effects of the drug to cell viability would be important.

Toxicity in Jurkat cells was first determined by propidium iodide incorporation. Some compounds (i.e., AGR1.103 and VSP3.1) were discarded from further analysis as they were toxic for cells. In a deeper analysis of cell toxicity, even if these compounds did not kill the cells, we checked whether they could alter the cell cycle of the cells. New Supplementary Fig. 2 includes a table (panel B) with the percentage of cells in each cell cycle phase, and no differences between any of the treatments tested were detected. 

Nevertheless, to clarify this issue the revised version of the figure also includes H2O2 and staurosporine stimuli to induce cell death and cell cycle alterations as controls of these assays.

(7) The flow data in Supplementary Figure 2 should be statistically analysed. 

Bar graphs corresponding to the old Supplementary Fig. 2 (new Supplementary Fig. 3) are shown in Fig. 3B. We have also incorporated the corresponding statistical analysis to this figure. 

(8) In general, the authors should revise the figure legends to ensure that critical details are added. 

We have carefully revised all the figure legends in the new version of the manuscript.

(9) Bar plots are very poor in showing the heterogeneity of the data. Individual data points should be shown whenever feasible. Superplot-type of representation is strongly advised (https://doi.org/10.1083/jcb.202001064).

We have carefully read the paper published by Lord S.J. and col. (Lord S. J. et al., J. Cell Biol. 2020) and we apply their recommendations for our TIRF-M data (see revised Fig.  2).

Author Response

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

eLife assessment

This valuable work provides a near-complete description of the mechanosensory bristles on the Drosophila melanogaster head and the anatomy and projection patterns of the bristle mechanosensory neurons that innervate them. The data presented are solid. The study has generated numerous invaluable resources for the community that will be of interest to neuroscientists in the field of circuits and behaviour, particularly those interested in mechanosensation and behavioural sequence generation.

We express our gratitude to the Reviewers for their valuable suggestions, which significantly enhanced the manuscript. The revisions were undertaken, not with the expectation of acceptance, but rather driven by our sincere belief that these revisions would enhance the manuscript's impact for future readers.

Public Reviews:

Reviewer #1 (Public Review):

Sensory neurons of the mechanosensory bristles on the head of the fly project to the sub esophageal ganglion (SEZ). In this manuscript, the authors have built on a large body of previous work to comprehensively classify and quantify the head bristles. They broadly identify the nerves that various bristles use to project to the SEZ and describe their region-specific innervation in the SEZ. They use dye-fills, clonal labelling, and electron microscopic reconstructions to describe in detail the phenomenon of somatotopy - conserved peripheral representations within the central brain - within the innervation of these neurons. In the process they develop novel tools to access subsets of these neurons. They use these to demostrate that groups of bristles in different parts of the head control different aspects of the grooming sequence.

Reviewer #2 (Public Review):

The authors combine genetic tools, dye fills and connectome analysis techniques to generate a "first-of-its-kind", near complete, synaptic resolution map of the head bristle neurons of Drosophila. While some of the BMN anatomy was already known based on previous work by the authors and other researchers, this is the first time a near complete map has been created for the head BMNs at electron microscopy resolution.

Strengths:

(1) The authors cleverly use techniques that allow moving back and forth between periphery (head bristle location) and brain, as well as moving between light microscopy and electron microscopy data. This allows them to first characterize the pathways taken by different head BMNs to project to the brain and also characterize anatomical differences among individual neurons at the level of morphology and connectivity.

(2) The work is very comprehensive and results in a near complete map of all I’m head BMNs.

(3) Authors also complement this anatomical characterization with a first-level functional analysis using optogenetic activation of BMNs that results in expected directed grooming behavior.

Weaknesses:

(1) The clustering analysis is compelling but cluster numbers seem to be arbitrarily chosen instead of by using some informed metrics.

We made revisions to the manuscript that address this concern. Please see our response to “recommendations for authors” for a description of these revisions.

(2) It could help provide context if authors revealed some of the important downstream pathways that could explain optogenetics behavioral phenotypes and previously shown hierarchical organization of grooming sequences.

We made revisions to the manuscript that address this recommendation. Please see our response to “recommendations for authors” for a description of these revisions.

(3) In contrast to the rigorous quantitative analysis of the anatomical data, the behavioral data is analyzed using much more subjective methods. While I do not think it is necessary to perform a rigorous analysis of behaviors in this anatomy focused manuscript, the conclusions based on behavioral analysis should be treated as speculative in the current form e.g. calling "nodding + backward walking" as an avoidance response is not justified as it currently stands. Strong optogenetic activation could lead to sudden postural changes that due to purely biomechanical constraints could lead to a couple of backward steps as seen in the example videos. Moreover since the quantification is manual, it is not clear what the analyst interprets as backward walking or nodding. Interpretation is also concerning because controls show backward walking (although in fewer instances based on subjective quantification).

While unbiased machine vision-based methods would nicely complement the present work, this type of analysis is not yet working to distinguish between different head grooming movements. Therefore, we are currently limited to manual annotation for our behavioral analysis. That said, we do not believe that our manual annotation is subjective. The grooming movements that we examine in this work are distinguishable from each other through frame-by-frame manual annotation of video at 30 fps. Our annotation of the grooming and backward motions performed by flies are based on previous publications that established a controlled vocabulary defining each movement (Hampel et al., 2020a, 2017, 2015; Seeds et al., 2014). In this work, we added head nodding to this controlled vocabulary that is described in the Materials and methods. We have added additional text to the third paragraph of the Material and methods section entitled “Behavioral analysis procedures” that we hope better describes our behavioral analysis. This description now reads:

Head nodding was annotated when the fly tilted its head downward by any amount until it returned its head back in its original position. This movement often occurred in repeated cycles. Therefore, the “start” was scored at the onset of the first forward movement and the “stop” when the head returned to its original position on the last nod.

We do not make any firm conclusions about the head movements (nodding) and backwards motions. We refer to nodding as a descriptive term that would allow the reader to better understand what the behavior looks like. We make no firm conclusions about any behavioral functional role that either the nodding or the backward motions might have, with the exception of nodding in the context of grooming. We only suggest that the behaviors appear to be avoidance responses. Furthermore, backward walking was not mentioned. Instead we refer to backward motions. We are only reporting our annotations of these movements that do occur, and are significantly different from controls. We speculate that these could be avoidance responses based on support from the literature. Future studies will be required to understand whether these movements serve real behavioral roles.

Summary:

The authors end up generating a near-complete map of head BMNs that will serve as a long-standing resource to the Drosophila research community. This will directly shape future experiments aimed at modeling or functionally analyzing the head grooming circuit to understand how somatotopy guides behaviors.

Reviewer #3 (Public Review):

Eichler et al. set out to map the locations of the mechanosensory bristles on the fly head, examine the axonal morphology of the bristle mechanosensory neurons (BMNs) that innervate them, and match these to electron microscopy reconstructions of the same BMNs in a previously published EM volume of the female adult fly brain. They used BMN synaptic connectivity information to create clusters of BMNs that they show occupy different regions of the subesophageal zone brain region and use optogenetic activation of subsets of BMNs to support the claim that the morphological projections and connectivity of defined groups of BMNs are consistent with the parallel model for behavioral sequence generation.

The authors have beautifully cataloged the mechanosensory bristles and the projection paths and patterns of the corresponding BMN axons in the brain using detailed and painstaking methods. The result is a neuroanatomy resource that will be an important community resource. To match BMNs reconstructed in an electron microscopy volume of the adult fly brain, the authors matched clustered reconstructed BMNs with light-level BMN classes using a variety of methods, but evidence for matching is only summarized and not demonstrated in a way that allows the reader to evaluate the strength of the evidence. The authors then switch from morphology-based categorization to non-BMN connectivity as a clustering method, which they claim demonstrates that BMNs form a somatotopic map in the brain. This map is not easily appreciated, and although contralateral projections in some populations are clear, the distinct projection zones that are mentioned by the authors are not readily apparent. Because of the extensive morphological overlap between connectivity-based clusters, it is not clear that small projection differences at the projection level are what determines the post-synaptic connectivity of a given BMN cluster or their functional role during behavior. The claim the somatotopic organization of BMN projections is preserved among their postsynaptic partners to form parallel sensory pathways is not supported by the result that different connectivity clusters still have high cosine similarity in a number of cases (i.e. Clusters 1 and 3, or Clusters 1 and 2). Finally, the authors use tools that were generated during the light-level characterization of BMN projections to show that specifically activating BMNs that innervate different areas of the head triggers different grooming behaviors. In one case, activation of a single population of sensory bristles (lnOm) triggers two different behaviors, both eye and dorsal head grooming. This result does not seem consistent with the parallel model, which suggests that these behaviors should be mutually exclusive and rely on parallel downstream circuitry.

We made revisions to the manuscript that address this recommendation. Please see our response to “recommendations for authors” for a description of these revisions.

This work will have a positive impact on the field by contributing a complete accounting of the mechanosensory bristles of the fruit fly head, describing the brain projection patterns of the BMNs that innervate them, and linking them to BMN sensory projections in an electron microscopy volume of the adult fly brain. It will also have a positive impact on the field by providing genetic tools to help functionally subdivide the contributions of different BMN populations to circuit computations and behavior. This contribution will pave the way for further mechanistic study of central circuits that subserve grooming circuits.

Recommendations for the authors:

All three reviewers appreciated the work presented in this manuscript. There were also a few overlapping concerns that were raised that are summarised below, should the authors wish to address them:

Somatotopy: We recommend that the authors describe the extent of prior knowledge in more detail to highlight their contribution better.

We made revisions that better highlight the extent of prior knowledge about somatotopy. We describe how previous studies showed bristle mechanosensory neurons in insects are somatotopically organized, but these studies were not comprehensive descriptions of complete somatotopic maps for the head or body. To our knowledge, our study provides the first comprehensive and synaptic resolution somatotopic map of a head for any animal. This sets the stage for the complete definition of the interface between somatotopically-organized mechanosensory neurons and postsynaptic circuits, which has broad implications for future studies on aimed grooming, and mechanosensation in general. Below we itemize revisions to the Introduction, Discussion, and Figures to provide a clearer statement of the significance of our study as it relates to somatotopy.

(1) Newly added Figure 1 – figure supplement 1 more explicitly grounds the study in somatotopy, providing a working model of the organization of the circuit pathways that produce the grooming sequence. This model features somatotopy as shown in Figure 1 – figure supplement 1C.

(2) Figure 1 – figure supplement 1 is incorporated into the Introduction in the second, third, and fourth paragraphs, the first paragraph of the Results section titled “Somatotopically-organized parallel BMN pathways”, and the second and third paragraphs of the last Discussion section titled “Parallel circuit architecture underlying the grooming sequence”.

(3) We added text to the end of the fourth paragraph of the Introduction that now reads: “In this model, parallel-projecting mechanosensory neurons that respond to stimuli at specific locations on the head or body could connect with somatotopically-organized parallel circuits that elicit grooming of those locations (Figure 1 – figure supplement 1A-C). The previous discovery of a mechanosensory-connected circuit that elicits aimed grooming of the antennae provides evidence of this organization (Hampel 2015). However, the extent to which distinct circuits elicit grooming of other locations is unknown, in part, because the somatotopic projections of the mechanosensory neurons have not been comprehensively defined for the head or body.”

(4) There is a Discussion section that further explains the extent of prior knowledge and our contributions on somatotopy that is titled “A synaptic resolution somatotopic map of the head BMNs”. Additionally, the previous version of this section had a paragraph on the broader implications of our work as it relates to somatotopy across species. In light of the reviewer comments, we decided to make this paragraph into its own Discussion section to better highlight the broader significance of our work. This section is titled “First synaptic resolution somatotopic map of the head”.

The somatotopy isn't overtly obvious - perhaps they could try mapping presynaptic sites and provide landmarks to improve visualisation.

We made the following revisions to better highlight the head BMN somatotopy. One point of confusion from the previous manuscript version stemmed from us not explicitly defining the somatotopic organization that we observed. There seemed to be confusion that we were defining the head somatotopy based only on the small projection differences among BMNs from neighboring head locations. While we believe that these small differences indeed correspond to somatotopy, we failed to highlight that there are overt differences in the brain projections of BMNs from distant locations on the head. For example, Figure 5B (right panel) shows the distinct projections between the LabNv (brown) and AntNv (blue) BMNs that innervate bristles on the ventral and dorsal head, respectively. Thus, BMN types innervating neighboring bristles show overlapping projections with small projection differences, whereas those innervating distant bristles show non overlapping projections into distinct zones.

Our analysis of postsynaptic connectivity similarity also shows somatotopic organization among the BMN postsynaptic partners, as BMN types innervating the same or neighboring bristle populations show high connectivity similarity (Figure 8, old Figure 7). Below we highlight major revisions to the text and Figures that hopefully better reveal the head somatotopy.

(1) In the last paragraph of the Introduction we added text that explicitly frames the experiments in terms of somatotopic organization: “This reveals somatotopic organization, where BMNs innervating neighboring bristles project to the same zones in the CNS while those innervating distant bristles project to distinct zones. Analysis of the BMN postsynaptic connectome reveals that neighboring BMNs show higher connectivity similarity than distant BMNs, providing evidence of somatotopically organized postsynaptic circuit pathways.”

(2) We mention an example of overt somatotopy from Figure 5 in the Results section titled “EM-based reconstruction of the head BMN projections in a full adult brain”. The text reads “For example, BMNs from the Eye- and LabNv have distinct ventral and anterior projections, respectively. This shows how the BMNs are somatotopically organized, as their distinct projections correspond to different bristle locations on the head (Figure 5B,C).”

(3) In new Figure 8 (part of old Figure 7), we modified panels that correspond to the cosine similarity analysis of postsynaptic connectivity. The major revision was to plot the cosine similarity clusters onto the head bristles so that the bristles are now colored based on their clusters (C). This shows how neighboring BMNs cluster together, and therefore show similar postsynaptic connectivity. We believe that this provides a nice visualization of somatotopic organization in BMN postsynaptic connectivity. We also added the clustering dendrogram as recommended by Reviewer #2 (Figure 8A).

(4) In new Figure 8, we added new panels (D-F) that summarize our anatomical and connectomic analysis showing different somatotopic features of the head BMNs. Different BMN types innervate bristles at neighboring and distant proximities (D). BMNs that innervate neighboring bristles project into overlapping zones (E, example of reconstructed BM-Fr and -Ant neurons with non-overlapping BM-MaPa neurons) and show postsynaptic connectivity similarity (F, example connectivity map of three BM types on cosine similarity data).

(5) To accompany the new Figure 8D-F panels, we added a paragraph to summarize the different somatotopic features of the head BMNs that were identified based on our anatomical and connectomic analysis. This is the last paragraph in the Results section titled “Somatotopically-organized parallel BMN pathways”:

Our results reveal head bristle proximity-based organization among the BMN projections and their postsynaptic partners to form parallel mechanosensory pathways. BMNs innervating neighboring bristles project into overlapping zones in the SEZ, whereas those innervating distant bristles project to distinct zones (example of BM-Fr, -Ant, and -MaPa neurons shown in Figure 8D,E). Cosine similarity analysis of BMN postsynaptic connectivity revealed that BMNs innervating the same bristle populations (same types) have the highest connectivity similarity. Figure 8F shows example parallel connections for BM-Fr, -Ant, and -MaPa neurons (vertical arrows), where the edge width indicates the number of synapses from each BMN type to their major postsynaptic partners. Additionally, BMNs innervating neighboring bristle populations showed postsynaptic connectivity similarity, while BMNs innervating distant bristles show little or none. For example, BM-Fr and -Ant neurons have connections to common postsynaptic partners, whereas BM-MaPa neurons show only weak connections with the main postsynaptic partners of BM-Fr or -Ant neurons (Figure 8F, connections under 5% of total BMN output omitted). These results suggest that BMN somatotopy could have different possible levels of head spatial resolution, from specific bristle populations (e.g. Ant bristles), to general head areas (e.g. dorsal head bristles).

We also refer to Figure 8D-F to illustrate the different somatotopic features in the Discussion. These references can be found in the following Discussion sections titled “A synaptic resolution somatotopic map of the head BMNs (fourth paragraph)”, and “Parallel circuit architecture underlying the grooming sequence (second paragraph)”.

(6) In addition to improving the Figures, we provide additional tools that enable readers to explore the BMN somatotopy in a more interactive way. That is, we provide 5 different FlyWire.ai links in the manuscript Results section that enable 3D visualization of the different reconstructed BMNs (e.g. FlyWire.ai link 1).

Note: In working on old Figure 7 to address this Reviewer suggestion, we also reordered panels A-E. We believe that this was a more logical ordering than in the previous draft. These panels are now the only data shown in Figure 7, as the cosine similarity analysis is now in Figure 8. We hope that splitting these panels into two Figures will improve manuscript readability.

Light EM Mapping: A better description of methods by which this mapping was done would be helpful. Perhaps the authors could provide a few example parallel representations of the EM and light images in the main figure would help the reader better appreciate the strength of their approach.

We have done as the Reviewers suggested and added panels to Figure 6 that show examples of the LM and EM image matching (Figure 6A,B). We added two examples that used different methods for labeling the LM imaged BMNs, including MCFO labeling of an individual BM-InOc neuron and driver line labeling of a major portion of BM-InOm neurons using InOmBMN-LexA. These panels are referred to in the first paragraph of the Results section titled “Matching the reconstructed head BMNs with their bristles”. Note that examples for all LM/EM matched BMN types are shown in Figure 6 – figure supplement 2.

We had provided Figure 6 – figure supplement 2 in the reviewed manuscript that shows all the above requested “parallel representations of the EM and light images”. However, the Reviewer critiques made us realize that the purpose of this figure supplement was not clearly indicated. Therefore, we have revised Figure 6 – figure supplement 2 and its legend to make its purpose clearer. First, we changed the legend title to better highlight its purpose. The legend is now titled: “Matching EM reconstructed BMN projections with light microscopy (LM) imaged BMNs that innervate specific bristles”. Second, we added label designations to the figure panel rows that highlight the LM and EM comparisons. That is, the rows for light microscopy images of BMNs are indicated with LM and the rows for EM reconstructed BMN images are labeled with EM. Reviewer #3 had indicated that it was not clear what labeling methods were used to visualize the LM imaged BM-InOm neurons in Figure 6 – figure supplement 2N. Therefore, we added text to the figure and the legend to better highlight the different methods used. Panels A and B were also cropped to accommodate the above mentioned revisions.

The manuscript also provides an extensive Materials and methods section that describes the different lines of evidence that were used to assign the reconstructed BMNs as specific types. We changed the title to better highlight the purpose of this methods section to “Matching EM reconstructed BMN projections with light microscopy imaged BMNs that innervate specific bristles”. The evidence used to support the assignment of the different BMN types is also summarized in Figure 6 – figure supplement 3.

Parallel circuit model: The authors motivate their study with this. We're recommending that they define expectations of such circuitry, its alternatives (including implications for downstream pathways), and behavior before they present their results. We're also recommending that they interpret their behavioural results in the context of these circuits.

Our primary motivation for doing the experiments described in this manuscript was to help define the neural circuit architecture underlying the parallel model that drives the Drosophila grooming sequence. This manuscript provides a comprehensive assessment of the first layer of this circuit architecture. A byproduct of this work is a contribution that offers immediate utility and significance to the Drosophila connectomics community. Namely, the description of the majority of mechanosensory neurons on the head, with their annotation in the recently released whole brain connectome dataset (FlyWire.ai). In writing this manuscript, we tried to balance both of these things, which was difficult to write. We very much appreciate the Reviewers' comments that have highlighted points of confusion in our original draft. We hope that the revised draft is now clearer and more logically presented. We have made revisions to the text and provided a new figure supplement (Figure 1 - figure supplement 1) and new panels in Figure 8. Below we highlight the major revisions.

(1) The Introduction was revised to more explicitly ground the study in the parallel model, while also removing details that were not pertinent to the experiments presented in the manuscript.

The first paragraph introduces different features of the parallel model. To better focus the reader on the parts of the model that were being assessed in the manuscript, we removed the following sentences: “Performance order is established by an activity gradient among parallel circuits where earlier actions have the highest activity and later actions have the lowest. A winner-take-all network selects the action with the highest activity and suppresses the others. The selected action is performed and then terminated to allow a new round of competition and selection of the next action.” Note that these sentences are included in the third and fourth paragraphs of the last Discussion section titled “Parallel circuit architecture underlying the grooming sequence”.

The first paragraph of the Introduction now introduces a bigger picture view of the model that emphasizes the two main features: 1) a parallel circuit architecture that ensures all mutually exclusive actions to be performed in sequence are simultaneously readied and competing for output, and 2) hierarchical suppression among the parallel circuits, where earlier actions suppress later actions.

(2) Newly added Figure 1 – figure supplement 1 provides a working model of grooming (Reviewer # 1 suggestion). We now more strongly emphasize that the study aimed to define the parallel neural circuit architecture underlying the grooming sequence, focusing on the mechanosensory layer of this architecture. In particular, we refer to the new Figure 1 – figure supplement 1 that has been added to better convey the hypothesized grooming neural circuit architecture. Figure 1 – figure supplement 1 is incorporated into the Introduction (paragraphs two, three, and four), Results section titled “Somatotopically-organized parallel BMN pathways (first paragraph)”, and last Discussion section titled “Parallel circuit architecture underlying the grooming sequence (second and third paragraphs)”.

(3) New panels in Figure 8 update the model of parallel circuit organization as it relates to somatotopy (D-F). These panels show the parallel circuits hypothesized by the model, but also indicate convergence, with different possible levels of head resolution for these circuits. We describe above where these panels are referenced in the text.

(4) We added a new paragraph in the last Discussion section titled “Parallel circuit architecture underlying the grooming sequence” that better incorporates the results from this manuscript into the working model of grooming. This paragraph is shown below.

Here we define the parallel architecture of BMN types that elicit the head grooming sequence that starts with the eyes and proceeds to other locations, such as the antennae and ventral head. The different BMN types are hypothesized to connect with parallel circuits that elicit grooming of specific locations (described above and shown in Figure 1 – figure supplement 1A,C). Indeed, we identify distinct projections and connectivity among BMNs innervating distant bristles on the head, providing evidence supporting this parallel architecture (Figure 8D-F). However, we also find partially overlapping projections and connectivity among BMNs innervating neighboring bristles. Further, optogenetic activation of BMNs at specific head locations elicits grooming of both those locations and neighboring locations (Figure 9). These findings raise questions about the resolution of the parallel architecture underlying grooming. Are BMN types connected with distinct postsynaptic circuits that elicit aimed grooming of their corresponding bristle populations (e.g. Ant bristles)? Or are neighboring BMN types that innervate bristles in particular head areas connected with circuits that elicit grooming of those areas (e.g. dorsal or ventral head)? Future studies of the BMN postsynaptic circuits will be required to define the resolution of the parallel pathways that elicit aimed grooming.

Aside from this summary of major concerns, the detailed recommendations are attached below.

Reviewer #1 (Recommendations For The Authors):

I appreciate the quality and exhaustive body of work presented in this manuscript. I have a few comments that the authors may want to consider:

(1) The authors motivate this study by posing that it would allow them to uncover whether the complex grooming behaviour of flies followed a parallel model of circuit function. It would have been nice to have been introduced to what the alternative model might be and what each would mean for organisation of the circuit architecture. Some guiding schematics would go a long way in illustrating this point. Modifying the discussion along these lines would also be helpful.

We made several revisions to the manuscript that address this recommendation. Among these revisions, we added Figure 1 – figure supplement 1 that includes a working model for grooming. Please see above for a description of these revisions.

(2) The authors mention the body of work that has mapped head bristles and described somatotopy. It would be useful to discuss in more detail what these studies have shown and highlight where the gaps are that their study fills.

We made several revisions to the manuscript that address this recommendation. Please see above for a description of these revisions.

(3) The dye-fills and reconstructions that are single colour could use a boundary to demarcate the SEZ. This would help in orienting the reader.

We agree with Reviewer #1 that Figure 4 and its supplements could use some indicator that would orient the reader with respect to the dye filled or stochastically labeled neurons. The images are of the entire SEZ in the ventral brain, and in the case of some panels, the background staining enables visualization of the brain (e.g. Figure 4H,M,N. To help orient the reader in this region, we added a dotted line to indicate the approximate SEZ midline. This also enables the reader to more clearly see which of the BMN types cross the midline.

Midline visual guides were added for Figure 4, Figure 4 – figure supplement 2, Figure 4 – figure supplement 3, Figure 4 – figure supplement 4, Figure 4 – figure supplement 5, Figure 4 – figure supplement 6, Figure 4 – figure supplement 7, Figure 4 – figure supplement 8, Figure 6 – figure supplement 2.

(4) The comparison between the EM and the fills/clones are not obvious. And particularly because they are not directly determined, it would be nice to have the EM reconstruction alongside the dye-fills. This would work very nicely in the supplementary figure with the multiple fills of the same bristles. I think this would really drive home the point.

We made several revisions to the manuscript that address this recommendation. Please see above for a description of these revisions.

(5) Are there unnoticed black error-bars floating around in many of the gray-scale images?

The black bars were masking white scale bars in the images. We have removed the black bars and remade the images without scale bars. This was done for the following Figures: Figure 4, Figure 4 – figure supplement 2, Figure 4 – figure supplement 3, Figure 4 – figure supplement 4, Figure 4 – figure supplement 5, Figure 4 – figure supplement 6, Figure 4 – figure supplement 7, Figure 4 – figure supplement 8, Figure 6 – figure supplement 2.

Reviewer #2 (Recommendations For The Authors):

(1) The only point in the paper I found myself going back and forth between methods/supp and text was when authors discuss about the clustering. I think it would help the reader if a few sentences about cosine clustering used for connectivity based clustering were included in the main text. Also, for NBLAST hierarchical clustering, it would help if some informed metrics could be used for defining cluster numbers (e.g. Braun et al, 2010 PLOS ONE shows how Ward linkage cost could be used for hierarchical clustering).

Depending on where the cut height is placed on the dendrogram for cosine similarity of BMNs, different features of the BMN type postsynaptic connectivity are captured. As the number of clusters is increased (lower cut height), clustering is mainly among BMNs of the same type, showing that these BMNs have the highest connectivity similarity. As the number of clusters is reduced (higher cut height), BMNs innervating neighboring bristles on the head are clustered, revealing three general clusters corresponding to the dorsal, ventral, and posterior head. This reveals somatotopy based clustering among same and neighboring BMN types. The cut height shown in Figure 8 and Figure 8 – figure supplement 2 was chosen because it highlighted both of these features.

The NBLAST clustering shows similar results to the connectivity based clustering with respect to neighboring and distant BMN types. As the number of clusters increases BMNs of the same type are clustered, and these types can be further subdivided into morphologically distinct subtypes. As the number of clusters is reduced, the clustering captures neighboring BMNs. Thus, neighboring BMN types showed high morphology similarity (and proximity) with each other, and low similarity with distant BMN types.

Please see our responses to a Reviewer #3 critique below for further description of the clustering results.

On the same lines it would help if the clustering dendrograms were included in the main figure.

We thank Reviewer #2 for this comment. We have added the dendrogram to Figure 8A, a change that we feel makes this Figure much easier to understand.

(2) It could help provide intuition if the authors revealed some of the downstream targets and their implication in explaining the behavioral phenotypes.

While this will be the subject of at least two forthcoming manuscripts, we have added text to the present manuscript that provides insight into BMN postsynaptic targets. Our previous work (Hampel et al. 2015) described a mechanosensory connected neural circuit that elicits grooming of the antennae. While this previous study demonstrated that the Johnston’s organ mechanosensory neurons are synaptically and functionally connected with this circuit, our preliminary analysis indicates that it is also connected with BM-Ant neurons. We hypothesize that there are additional such circuits that are responsible for eliciting grooming of other head locations.

To better highlight potential downstream targets in the manuscript, we now mention the antennal circuit in the Introduction. This text reads: In this model, parallel-projecting mechanosensory neurons that respond to stimuli at specific locations on the head or body could connect with somatotopically-organized parallel circuits that elicit grooming of those locations (Figure 1 – figure supplement 1A-C). The previous discovery of a mechanosensory-connected circuit that elicits aimed grooming of the antennae provides evidence of this organization (Hampel 2015). However, the extent to which distinct circuits elicit grooming of other locations is unknown, in part, because the somatotopic projections of the mechanosensory neurons have not been comprehensively defined for the head or body.

There is also text in the Discussion that addresses this Reviewer comment. It describes the antennal circuit and mentions the possibility that other similar circuits may exist. This can be found in the third paragraph of the section titled “Circuits that elicit aimed grooming of specific head locations”.

(3) Authors find that opto activation of BMNs leads to grooming of targeted as well as neighboring areas. Is there any sequence observed here? i.e. first clean targeted area and then clean neighboring area? I wonder if the answer to this is something as simple as common post-synaptic targets which is essentially reducing the resolution of the BMN sensory map. Some more speculation on this interesting result could be helpful.

We appreciate and agree with this point from Reviewer #2, and have tried to better emphasize the possible implications for grooming that the overlapping projections and connectivity among BMNs innervating neighboring bristles may have. This is now better addressed in the Results and Discussion sections. Below we highlight where this is addressed:

(1) In the second paragraph of the Results section titled “Activation of subsets of head BMNs elicits aimed grooming of specific locations” we added text that suggests the possibility that grooming of the stimulated and neighboring locations could be due to the overlapping projections and connectivity. This text reads: This suggested that head BMNs elicit aimed grooming of their corresponding bristle locations, but also neighboring locations. This result is consistent with our anatomical and connectomic data indicating that BMNs innervating neighboring bristles show overlapping projections and postsynaptic connectivity similarity (see Discussion).

(2) In the fourth paragraph of the Discussion section titled “A synaptic resolution somatotopic map of the head BMNs”, we added a sentence to the end of the fourth paragraph that alludes to further discussion of this topic. This sentence reads: This overlap may have implications for aimed grooming behavior. For example, neighboring BMNs could connect with common neural circuits to elicit grooming of overlapping locations (discussed more below).

(3) In the fourth paragraph of the Discussion section titled “Circuits that elicit aimed grooming of specific head locations” there is a paragraph that mentions the possibility of mechanosensory convergence onto common postsynaptic circuits to promote grooming of the stimulated area, along with neighboring areas. This paragraph is below.

We find that activation of specific BMN types elicits both aimed grooming of their corresponding bristle locations and neighboring locations. This suggests overlap in the locations that are groomed with the activation of different BMN types. Such overlap provides a means of cleaning the area surrounding the stimulus location. Interestingly, our NBLAST and cosine similarity analysis indicates that neighboring BMNs project into overlapping zones in the SEZ and show common postsynaptic connectivity. Thus, we hypothesize that neighboring BMNs connect with common neural circuits (e.g. antennal grooming circuit) to elicit overlapping aimed grooming of common head locations.

(4) In the new second paragraph of the Discussion section titled “Parallel circuit architecture underlying the grooming sequence” we further discuss the issue of the BMN “sensory map. This paragraph is below.

Here we define the parallel architecture of BMN types that elicit the head grooming sequence that starts with the eyes and proceeds to other locations, such as the antennae and ventral head. The different BMN types are hypothesized to connect with parallel circuits that elicit grooming of specific locations (described above and shown in Figure 1 – figure supplement 1A,C). Indeed, we identify distinct projections and connectivity among BMNs innervating distant bristles on the head, providing evidence supporting this parallel architecture (Figure 8D-F). However, we also find partially overlapping projections and connectivity among BMNs innervating neighboring bristles. Further, optogenetic activation of BMNs at specific head locations elicits grooming of both those locations and neighboring locations (Figure 9). These findings raise questions about the resolution of the parallel architecture underlying grooming. Are BMN types connected with distinct postsynaptic circuits that elicit aimed grooming of their corresponding bristle populations (e.g. Ant bristles)? Or are neighboring BMN types that innervate bristles in particular head areas connected with circuits that elicit grooming of those areas (e.g. dorsal or ventral head)? Future studies of the BMN postsynaptic circuits will be required to define the resolution of the parallel pathways that elicit aimed grooming.

(4) If authors were to include a summary table that shows all known attributes about BMN type as columns that could be very useful as a resource to the community. Table columns could include attributes like "bristle name", "nerve tract", "FlyWire IDs of all segments corresponding to the bristle class". "split-Gal4 line or known enhancer" , etc.

We provided a table that includes much of this information after the manuscript had already gone out for review. We regret that this was not available. This is now provided as Supplementary file 3. This table provides the following information for each reconstructed BMN: BMN name, bristle type, nerve, flywire ID, flywire coordinates, NBLAST cluster (cut height 1), NBLAST cluster (cut height 5), and cosine cluster (cut height 4.5). Note that the driver line enhancers for targeting specific BMN types are shown in Figure 3I.

Specific Points:

Figure 4C-V:

• I find it a bit difficult to distinguish ipsi- from contra-lateral projections. Maybe indicate the midline as a thin, stippled line?

We thank the Reviewer #2 for this suggestion. We have now added lines in the panels in Figure 4C-V to indicate the approximate location of the midline. We also added lines to the Figure 4 – figure supplements as described above.

I think this Fig reference is wrong "the red-light stimulus also elicited backward motions with control flies (Figure 6B,C, control, black trace, Video 5)." should be Fig 8B,C

We have fixed this error.

Reviewer #3 (Recommendations For The Authors):

Introduction:

Motivating this study in terms of understanding the neural mechanisms that execute the parallel model seems to overstate what you will achieve with the current study. If you want to motivate it this way, I suggest focusing on the grooming sequence of the head along (eyes, antennae, proboscis).

We made several revisions to the manuscript that address this recommendation. Please see above for a description of these revisions. Please note that many of the revisions focus on the head grooming sequence. We also made minor revisions to the Introduction that further emphasize the focus on head grooming.

Results:

Figure 1. Please indicate that this is a male fly in either the figure title or in the figure itself.

We added a male symbol to Figure 1A.

Figure 3. Panel J is referenced in the main body text and in the figure caption, but there is no Fig 3J.

Panel J is shown in the upper right corner of Figure 3. We realize that the placement of this panel is not ideal, but this was the only place that we could fit it. Additionally, the panel works nicely at that location to better enable comparison with panel C. We have revised the text in the Figure 3 legend to better highlight the location of this Figure panel: “Shown in the upper right corner of the figure are the aligned expression patterns of InOmBMN-LexA (red), dBMN-spGAL4 (green), and TasteBMN-spGAL4 (brown).”

We also added text to a sentence in the results section entitled “Head BMNs project into discrete zones in the ventral brain” that indicates the panel location. This text reads: To further visualize the spatial relationships between these projections, we computationally aligned the expression patterns of the different driver lines into the same brain space (Figure 3J, upper right corner).

Matching the BMNs to EM reconstructions: why cut the dendrogram at H=5? Would be better to determine cluster number using an unbiased method.

To match the morphologically distinct EM reconstructed BMNs to their specific bristles, we relied on different lines of evidence, including NBLAST results (discussed more below), dye fill/stochastic labeling/driver line labeling matches, published morphology, nerve projection, bristle number, proximity to other BMNs, and postsynaptic connectivity (summarized in Figure 6 – figure supplement 3). The following Materials and methods section provides a detailed description of the evidence used to assign each BMN type in “Matching EM reconstructed BMN projections with light microscopy imaged BMNs that innervate specific bristles”. In many cases, BMN type could be assigned with confidence solely based on morphological comparisons with our light level data (e.g. dye fills), in conjunction with bristle counts to indicate an expected number of BMNs showing similar morphology. Thus, the LM/EM matches and NBLAST clustering were largely complementary.

The EM reconstructed BMNs were matched as particular BMN types, in part based on examination of the NBLAST data at different cut heights. NBLAST clustering of the BMNs revealed general trends at higher and lower cut heights (Figure 6 – figure supplement 1A, Supplementary file 3). The lowest cut heights included mostly BMNs of the same type innervating the same bristle populations, and smaller clusters that subdivided into morphologically distinct subtypes (see Supplementary file 3 for clusters produced at cut height 1). This revealed that BMNs of the same type tended to show the highest morphological similarity with each other, but they also showed intratype morphological diversity. Higher cut heights produced clusters of BMNs innervating neighboring bristles populations (e.g. ventral head BMNs), showing high morphological similarity among neighboring BMN types.

We selected the cut height 5 shown in Figure 6 – figure supplement 1A,B because it captures examples of both same and neighboring type clustering. For example, it captures a cluster of mostly BM-Taste neurons (Cluster 16), and neighboring BMN types, including those from the dorsal head (Cluster 14) or ventral head (Cluster 15).

Based on reviewer comments, we realized that the way we wrote the BMN matching section in the Results indicated more reliance on the NBLAST clustering than what was actually necessary, distorting the way we actually matched the BMNs. Therefore, we softend the first couple of sentences to place less emphasis on the importance of the NBLAST. We also indicated that the readers can find the resulting clusters at different cut heights, referring to Figure 6 – figure supplement 1A and Supplementary file 3. The first two sentences of the first paragraph in the Results section titled “Matching the reconstructed head BMNs with their bristles” now read:

The reconstructed BMN projections were next matched with their specific bristle populations. The projections were clustered based on morphological similarity using the NBLAST algorithm (example clustering at cut height 5 shown in Figure 6 – figure supplement 1A,B, Supplementary file 3, FlyWire.ai link 2) (Costa et al., 2016). Clusters could be assigned as BMN types based on their similarity to light microscopy images of BMNs known to innervate specific bristles.

The number of reconstructed BMNs is remarkably similar to what is expected based on bristle counts for each group except for lnOm. Why do you think there is such a large discrepancy there?

We believe that there is a discrepancy between the number of reconstructed BM-InOm neurons and the number expected based on InOm bristle counts because these bristle counts were based on few flies and these numbers appear to be variable. We did not further investigate the numbers of InOm bristles in this manuscript because we only needed an estimate of their numbers, given that there is over an order of magnitude difference in the eye bristles versus any other head bristle population. Therefore, we could relatively easily conclude that the head BMNs were related to the InOm bristles, based on their sheer numbers and their morphology.

Figure 6 - figure supplement 2N, please describe these panels better. Main text says the upper image is from lnOmBMN-LexA, but the figure legend doesn't agree.

We have added text to the figure legend that now makes the contents of panel 2N clear to the reader. Further, we now indicate in the figure legend for each panel, the method used to obtain the labeled neurons (i.e. fill, MCFO, driver), to avoid similar confusion for the other panels.

Figure 6 - figure supplement 4D. How frequently is there a mismatch between the number of BMNs for a given type across hemispheres?

Although the full reconstruction of the BMNs on both sides of the brain was beyond the scope of this work, the BMNs on both sides have since been reconstructed and annotated (Schlegal et al. 2023). We plan to provide more analysis of BMNs on both sides of the brain in a forthcoming manuscript. However, the BMN numbers tend to show agreement on both sides of the brain. The table below shows a comparison between the two sides:

Author response table 1.

Figures 6 and 7. It would be helpful to include a reference brain in all panels that show cluster morphology. Without landmarks there is nothing to anchor the eye to allow the reader to see the described differences in BMN projection zones and patterns.

While we apologize for not making this specific change, we have made revisions to other parts of the manuscript to better highlight the somatotopic organization among the BMNs (revisions described above). Please note that we now provide FlyWire.ai publicly available links that enable readers to view the BMN projections in 3D. They can also toggle a brain mesh on and off to provide spatial reference.

"BMN somatotopic map": It would be helpful to show or describe in more detail what the unique branch morphology for each zone is. It is quite difficult to appreciate, as the groups also have a lot of overlap. Would the unique regions that the BMN groups innervate be easier to see if you plotted presynaptic sites by group? I am left unsure about whether there is a somatotopic map here.

We made several revisions to the manuscript that address this recommendation. Please see above for a description of these revisions. Please note that we did not examine the fine branch morphological differences between BMN types having overlapping projections. Showing these differences would require more extensive anatomical analysis that is beyond the scope of this work. For showing definitive somatotopy, we focused on the overt differences between BMNs innervating bristles at distant locations on the head.

Overall the strict adherence to the parallel model impacts the interpretation of the data. It would be helpful for the authors to discuss which aspects of the current study are consistent with the parallel model and which results are not consistent.

We made several revisions to the manuscript that address this recommendation. Please see above for a description of these revisions.

Discussion:

"Circuits that elicit aimed grooming of specific head locations": In the previous paragraph you mention "BMN types innervating neighboring bristle populations have overlapping projections into zones that correspond roughly to the dorsal, ventral, and posterior head. The overlap is likely functionally significant, as cosine similarity analysis revealed that neighboring head BMN types have common postsynaptic partners. However, overlap between neighboring BMN types is only partial, as they show differing projections and postsynaptic connectivity." Then in this paragraph, you say, "How do the parallel-projecting head BMNs interface with postsynaptic neural circuits to elicit aimed grooming of specific head locations? Different evidence supports the hypothesis that the BMNs connect with parallel circuits that each elicit a different aimed grooming movement (Seeds et al., 2014)." The overlapping postsynaptic BMN connectivity seems in conflict with the claim that the circuits are parallel.

We apologize for this confusion. We now better describe this apparent discrepancy between our results and the parallel model of grooming behavior. We made several revisions to the manuscript that address this recommendation. Please see above for a description of these revisions.

We have made additional changes to the manuscript:

(1) We added Supplementary file 2 that includes links for downloading the image stacks used to generate panels in Figure 1, Figure 2, Figure 3, Figure 4, and figure supplements for these figures. These image stacks are stored in the Brain Image Library (BIL). Rows in the spreadsheet correspond to each image stack. Columns provide information about each stack including: figure panels that each image stack contributed to, image stack title, DOI for each stack (link provides metadata for each stack and file download link), image stack file name, genotype of imaged fly, and information about image stack. References to this file have been made at different locations throughout the text and Figure legends. We also added a section on the BIL data in the Materials and methods entitled “Light microscopy image stack storage and availability”. Old Supplementary file 2 has been renamed Supplementary file 3.

(2) We added a new reference for FlyWire.ai (Dorkenwald et al. 2023) that was posted as a preprint during the revision of this manuscript.

Author response:

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

Reviewer #1 (Public Review): 

Summary: 

In this work, the authors examine the activity and function of D1 and D2 MSNs in dorsomedial striatum (DMS) during an interval timing task. In this task, animals must first nose poke into a cued port on the left or right; if not rewarded after 6 seconds, they must switch to the other port. Critically, this task thus requires animals to estimate if at least 6 seconds have passed after the first nose poke - this is the key aspect of the task focused on here. After verifying that animals reliably estimate the passage of 6 seconds by leaving on average after 9 seconds, the authors examine striatal activity during this interval. They report that D1-MSNs tend to decrease activity, while D2-MSNs increase activity, throughout this interval. They suggest that this activity follows a drift-diffusion model, in which activity increases (or decreases) to a threshold after which a decision (to leave) is made. The authors next report that optogenetically inhibiting D1 or D2 MSNs, or pharmacologically blocking D1 and D2 receptors, increased the average wait time of the animals to 10 seconds on average. This suggests that both D1 and D2 neurons contribute to the estimate of time, with a decrease in their activity corresponding to a decrease in the rate of

'drift' in their drift-diffusion model. Lastly, the authors examine MSN activity while pharmacologically inhibiting D1 or D2 receptors. The authors observe most recorded MSNs neurons decrease their activity over the interval, with the rate decreasing with D1/D2 receptor inhibition. 

Major strengths: 

The study employs a wide range of techniques - including animal behavioral training, electrophysiology, optogenetic manipulation, pharmacological manipulations, and computational modeling. The behavioral task used by the authors is quite interesting and a nice way to probe interval timing in rodents. The question posed by the authors - how striatal activity contributes to interval timing - is of importance to the field and has been the focus of many studies and labs; thus, this paper can meaningfully contribute to that conversation. The data within the paper is presented very clearly, and the authors have done a nice job presenting the data in a transparent manner (e.g., showing individual cells and animals). Overall, the manuscript is relatively easy to read and clear, with sufficient detail given in most places regarding the experimental paradigm or analyses used. 

We are glad our main points came through to the reviewer.  

Major weaknesses: 

I perceive two major weaknesses. The first is the impact or contextualization of their results in terms of the results of the field more broadly. More specifically, it was not clear to me how the authors are interpreting the striatal activity in the context of what others have observed during interval timing tasks. In other words - what was the hypothesis going into this experiment? Does observing increasing/decreasing activity in D2 versus D1 support one model of interval timing over another, or does it further support a more specific idea of how DMS contributes to interval timing? Or was the main question that we didn't know if D2 or D1 neurons had differential activity during interval timing? 

This is a helpful comment. Our hypothesis is that D1 and D2 MSNs had similar patterns of activity.  Our rationale is prior behavioral work from our group describing that blocking striatal D1 and D2 dopamine receptors had similar behavioral effects on interval timing (De Corte et al., 2019; Stutt et al., 2023), We rewrote our introduction with this idea in mind (Line 89)

“We and others have found that striatal MSNs encode time across multiple intervals by time-dependent ramping activity or monotonic changes in firing rate across a temporal interval (Emmons et al., 2017; Gouvea et al., 2015; Mello et al., 2015; Wang et al., 2018). However, the respective roles of D2-MSNs and D1-MSNs are unknown. Past work has shown that disrupting either D2-dopamine receptors (D2) or D1-dopamine receptors (D1) powerfully impairs interval timing by increasing estimates of elapsed time (Drew et al., 2007; Meck, 2006). Similar behavioral effects were found with systemic (Stutt et al., 2024) or local dorsomedial striatal D2 or D1 disruption (De Corte et al., 2019a). These data lead to the hypothesis that D2 MSNs and D1 MSNs have similar patterns of ramping activity across a temporal interval. 

We tested this hypothesis with a combination of optogenetics, neuronal ensemble recording, computational modeling, and behavioral pharmacology. We use a well-described mouse-optimized interval timing task (Balci et al., 2008; Bruce et al., 2021; Larson et al., 2022; Stutt et al., 2024; Tosun et al., 2016; Weber et al., 2023). Strikingly, optogenetic tagging of D2-MSNs and D1-MSNs revealed distinct neuronal dynamics, with D2-MSNs tending to increase firing over an interval and D1-MSNs tending to decrease firing over the same interval, similar to opposing movement dynamics (Cruz et al., 2022; Kravitz et al., 2010; Tecuapetla et al., 2016). MSN dynamics helped construct and constrain a four-parameter drift-diffusion computational model of interval timing, which predicted that disrupting either D2MSNs or D1-MSNs would increase interval timing response times. Accordingly, we found that optogenetic inhibition of either D2-MSNs or D1-MSNs increased interval timing response times. Furthermore, pharmacological blockade of either D2- or D1receptors also increased response times and degraded trial-by-trial temporal decoding from MSN ensembles. Thus, D2-MSNs and D1-MSNs have opposing temporal dynamics yet disrupting either MSN type produced similar effects on behavior. These data demonstrate how striatal pathways play complementary roles in elementary cognitive operations and are highly relevant for understanding the pathophysiology of human diseases and therapies targeting the striatum.”

In the second, I felt that some of the conclusions suggested by the authors don't seem entirely supported by the data they present, or the data presented suggests a slightly more complicated story. Below I provide additional detail on some of these instances. 

Regarding the results presented in Figures 2 and 3: 

I am not sure the PC analysis adds much to the interpretation, and potentially unnecessarily complicates things. In particular, running PCA on a matrix of noisy data that is smoothed with a Gaussian will often return PCs similar to what is observed by the authors, with the first PC being a line up/down, the 2nd PC being a parabola that is up/down, etc. Thus, I'm not sure that there is much to be interpreted by the specific shape of the PCs here. 

We are glad the reviewer raised this point. First, regarding the components in noisy data, what the reviewer says is correct, but usually, the variance explained by PC1 is small. This is the reason we include scree plots in our PC analysis (Fig 3B and Fig 6G). When we compare our PC1s to variance explained in random data, our PC1 variance is always stronger. We have now included this in our manuscript:

First, we generated random data and examined how much variance PC1 might generate. 

We added this to the methods (Line 634)

“The variance of PC1 was empirically compared against data generated from 1000 iterations of data from random timestamps with identical bins and kernel density estimates. Average plots were shown with Gaussian smoothing for plotting purposes only.”

These data suggested that our PC1 was stronger than that observed in random data (Line 183):

“PCA identified time-dependent ramping activity as PC1 (Fig 3A), a key temporal signal that explained 54% of variance among tagged MSNs (Fig 3B; variance for PC1 p = 0.009 vs 46 (44-49)% variance for PC1 derived from random data; Narayanan, 2016).”

And in the pharmacology data (Line 367):

“The first component (PC1), which explained 54% of neuronal variance, exhibited “time-dependent ramping”, or monotonic changes over the 6 second interval immediately after trial start (Fig 6F-G; variance for PC1 p = 0.001 vs 46 (45-47)% variance in random data; Narayanan, 2016).”

Second, we note that we have used this analysis extensively in the past, and PC1 has always been identified as a linear ramping in our work and in work by others (Line 179):

“Work by our group and others has uniformly identified PC1 as a linear component among corticostriatal neuronal ensembles during interval timing (Bruce et al., 2021; Emmons et al., 2020, 2019, 2017; Kim et al., 2017a; Narayanan et al., 2013; Narayanan and Laubach, 2009; Parker et al., 2014; Wang et al., 2018).”

Third, we find that PC1 is highly correlated to the GLM slope (Line 205):

“Trial-by-trial GLM slope was correlated with PC1 scores in Fig 3A-C (PC1 scores vs. GLM slope r = -0.60, p = 10-8).”

Fourth, our goal was not to heavily interpret PC1 – but to compare D1 vs. D2 MSNs, or compare population responses to D2/D1 pharmacology. We have now made this clear in introducing PCA analyses in the results (Line 177):

“To quantify differences in D2-MSNs vs D1-MSNs, we turned to principal component analysis (PCA), a data-driven tool to capture the diversity of neuronal activity (Kim et al., 2017a).”

Finally, despite these arguments the reviewer’s point is well taken. Accordingly, we have removed all analyses of PC2 from the manuscript which may have been overly interpretative. 

We have now removed language that interpreted the components, and we now find the discussion of PC1 much more data-driven. We have also removed much of the advanced PC analysis in Figure S9. Given our extensive past work using this exact analysis of PC1, we think PCA adds a considerable amount to our manuscript justified as the reviewer suggested. 

I think an alternative analysis that might be both easier and more informative is to compute the slope of the activity of each neuron across the 6 seconds. This would allow the authors to quantify how many neurons increase or decrease their activity much like what is shown in Figure 2.  

We agree – we now do exactly this analysis in Figure 3D. We now clarify this in detail, using the reviewer’s language to the methods (Line 648):

“To measure time-related ramping over the first 6 seconds of the interval, we used trial-by-trial generalized linear models (GLMs) at the individual neuron level in which the response variable was firing rate and the predictor variable was time in the interval or nosepoke rate (Shimazaki and Shinomoto, 2007). For each neuron, it’s time-related “ramping” slope was derived from the GLM fit of firing rate vs time in the interval, for all trials per neuron. All GLMs were run at a trial-by-trial level to avoid effects of trial averaging (Latimer et al., 2015) as in our past work (Bruce et al., 2021; Emmons et al., 2017; Kim et al., 2017b).”

And to the results (Line 194):

“To interrogate these dynamics at a trial-by-trial level, we calculated the linear slope of D2-MSN and D1-MSN activity over the first 6 seconds of each trial using generalized linear modeling (GLM) of effects of time in the interval vs trial-by-trial firing rate (Latimer et al., 2015).”

Relatedly, it seems that the data shown in Figure 2D *doesn't* support the authors' main claim regarding D2/D1 MSNs increasing/decreasing their activity, as the trial-by-trial slope is near 0 for both cell types. 

This likely refers to Figure 3D. The reviewer is correct that the changes in slope are small and near 0. Our goal was to show that D2-MSN and D1-MSN slopes were distinct – rather than increasing and decreasing. We have added this to the abstract (Line 46)

“We found that D2-MSNs and D1-MSNs exhibited distinct dynamics over temporal intervals as quantified by principal component analyses and trial-by-trial generalized linear models.”

We have clarified this idea in our hypothesis (Line 96):

“These data led to the hypothesis that D2 MSNs and D1 MSNs have similar patterns of ramping activity across a temporal interval.”

We have added this idea to the results (Line 194)

“To interrogate these dynamics at a trial-by-trial level, we calculated the linear slope of D2-MSN and D1-MSN activity over the first 6 seconds of each trial using generalized linear modeling (GLM) of effects of time in the interval vs trial-by-trial firing rate (Latimer et al., 2015). Nosepokes were included as a regressor for movement. GLM analysis also demonstrated that D2-MSNs had significantly different slopes (-0.01 spikes/second (-0.10 – 0.10)), which were distinct from D1MSNs (-0.20 (-0.47– -0.06; Fig 3D; F = 8.9, p = 0.004 accounting for variance between mice (Fig S3B); Cohen’s d = 0.8; power = 0.98; no reliable effect of sex (F = 0.02, p = 0.88) or switching direction (F = 1.72, p = 0.19)). We found that D2-MSNs and D1-MSNs had significantly different slopes even when excluding outliers (4 outliers excluded outside of 95% confidence intervals; F = 7.51, p = 0.008 accounting for variance between mice) and when the interval was defined as the time between trial start and the switch response on a trial-by-trial basis for each neuron (F = 4.3, p = 0.04 accounting for variance between mice). Trial-by-trial GLM slope was correlated with PC1 scores in Fig 3A-C (PC1 scores vs. GLM slope r = -0.60, p = 108). These data demonstrate that D2-MSNs and D1-MSNs had distinct slopes of firing rate across the interval and were consistent with analyses of average activity and PC1, which exhibited time-related ramping.”

And Line 215:

“In summary, we used optogenetic tagging to record from D2-MSNs and D1-MSNs during interval timing. Analyses of average activity, PC1, and trial-by-trial firingrate slopes over the interval provide convergent evidence that D2-MSNs and D1MSNs had distinct and opposing dynamics during interval timing. These data provide insight into temporal processing by striatal MSNs.”

And in the discussion (Line 415):

“We describe how striatal MSNs work together in complementary ways to encode an elementary cognitive process, interval timing. Strikingly, optogenetic tagging showed that D2-MSNs and D1-MSNs had distinct dynamics during interval timing. “

We have now included a new plot with box plots to make the differences in Figure 3D clear

Other reviewers requested additional qualitative descriptions of our data, and we have referred to increases / decreases in this context. 

Regarding the results in Figure 4: 

The authors suggest that their data is consistent with a drift-diffusion model. However, it is unclear how well the output from the model fits the activity from neurons the authors recorded. Relatedly, it is unclear how the parameters were chosen for the D1/D2 versions of this model. I think that an alternate approach that would answer these questions is to fit the model to each cell, and then examine the best-fit parameters, as well as the ability of the model to predict activity on trials held out from the fitting process. This would provide a more rigorous method to identify the best parameters and would directly quantify how well the model captures the data. 

We are glad the reviewer raised these points. Our goal was to use neuronal activity to fit behavioral activity, not the reverse. While we understand the reviewer’s point, we note that one behavioral output (switch time) can be encoded by many patterns of neuronal activity; thus, we are not sure we can use the model developed for behavior to fit diverse neuronal activity, or an ensemble of neurons. We have made this clear in the manuscript (Line 251):

“Our model aimed to fit statistical properties of mouse behavioral responses while incorporating MSN network dynamics. However, the model does not attempt to fit individual neurons’ activity, because our model predicts a single behavioral parameter – switch time – that can be caused by the aggregation of diverse neuronal activity.”

To attempt to do something close to what the reviewer suggested, we attempted to predict behavior directly from neuronal ensembles.  We have now made this clear in the methods on Line 682):

“Analysis and modeling of mouse MSN-ensemble recordings. Our preliminary analysis found that, for sufficiently large number of neurons (𝑵 > 𝟏𝟏), each recorded ensemble of MSNs on a trial-by-trial basis could predict when mice would respond. We took the following approach: First, for each MSN, we convolved its trial-by-trial spike train 𝑺𝒑𝒌(𝒕) with a 1-second exponential kernel 𝑲(𝒕) = 𝒘 𝒆-𝒕/𝒘 if 𝒕 > 𝟎 and 𝑲(𝒕) = 𝟎 if 𝒕 ≤ 𝟎 (Zhou et al., 2018; here 𝒘 = 𝟏 𝒔). Therefore, the smoothed, convolved spiking activity of neuron 𝒋 (𝒋 = 𝟏, 𝟐, … 𝑵),

tracks and accumulates the most recent (one second, in average) firing-rate history of the 𝒋-th MSN, up to moment 𝒕. We hypothesized that the ensemble activity

(𝒙𝟏(𝒕), 𝒙𝟐(𝒕), … , 𝒙𝑵(𝒕)), weighted with some weights 𝜷𝒋 , could predict the trial switch time 𝒕∗ by considering the sum

and the sigmoid 

that approximates the firing rate of an output unit. Here parameter 𝒌   indicates how fast 𝒙(𝒕) crosses the threshold 0.5 coming from below (if 𝒌 > 𝟎) or coming from above (if 𝒌 < 𝟎) and relates the weights 𝜷𝒋 to the unknowns 𝜷H𝒋 \= 𝜷𝒋/𝒌 and 𝜷H𝟎 \= −𝟎. 𝟓/𝒌. Next, we ran a logistic fit for every trial for a given mouse over the spike count predictor matrix 7𝒙𝟏(𝒕), 𝒙𝟐(𝒕), … , 𝒙𝑵(𝒕)9 from the mouse MSN recorded ensemble, and observed value 𝒕∗, estimating the coefficients 𝜷H𝟎 and 𝜷H𝒋, and so, implicitly, the weights 𝜷𝒋. From there, we compute the predicted switch time 𝒕∗𝒑𝒓𝒆𝒅 by condition 𝒙(𝒕) = 𝟎. 𝟓. Accuracy was quantified comparing the predicted accuracy within a 1 second window to switch time on a trial-by-trial basis (Fig S4).

And in the results (Line 254): 

We first analyzed trial-based aggregated activity of MSN recordings from each mouse (𝒙𝒋(𝒕)) where 𝒋 = 𝟏, … , 𝑵 neurons. For D2-MSN or D1-MSN ensembles of 𝑵 > 𝟏𝟏, we found linear combinations of their neuronal activities, with some 𝜷𝒋 coefficients,

that could predict the trial-by-trial switch response times (accuracy > 90%, Fig S4; compared with < 20% accuracy for Poisson-generated spikes of same trial-average firing rate). The predicted switch time 𝒕∗𝒑𝒓𝒆𝒅 was defined by the time when the weighted ensemble activity 𝒙(𝒕) first reached the value 𝒙) = 0.5. Finally, we built DDMs to account for this opposing trend (increasing vs decreasing) of MSN dynamics and for ensemble threshold behavior defining 𝒕∗𝒑𝒓𝒆𝒅; see the resulting model (Equations 1-3) and its simulations (Figure 4A-B).”

And we have added a new figure, Figure S4, that demonstrates these trial-by-trial predictions of switch response times.  

Note that we have included predictions from shuffled data similar to what the reviewer suggested based on shuffled data. Predictions are derived from neuronal ensembles on that trial; thus we could not apply a leave-one-out approach to trial-by-trial predictions.

These models are highly predictive for larger ensembles and poorly predictive for smaller ensembles.  We think this model adds to the manuscript and we are glad the reviewer suggested it. 

Relatedly, looking at the raw data in Figure 2, it seems that many neurons either fire at the beginning or end of the interval, with more neurons firing at the end, and more firing at the beginning, for D2/D1 neurons respectively. Thus, it's not clear to me whether the drift-diffusion model is a good model of activity. Or, perhaps the model is supposed to be related to the aggregate activity of all D1/D2 neurons? (If so, this should be made more explicit. The comment about fitting the model directly to the data also still stands).  

Our model was inspired by the aggregate activity.  We have now made this clear in the results (Line 227): 

“Our data demonstrate that D2-MSNs and D1-MSNs have opposite activity patterns. However, past computational models of interval timing have relied on drift-diffusion dynamics with a positive slope that accumulates evidence over time (Nguyen et al., 2020; Simen et al., 2011). To reconcile how these MSNs might complement to effect temporal control of action, we constructed a four-parameter drift-diffusion model (DDM). Our goal was to construct a DDM inspired by average differences in D2MSNs and D1-MSNs that predicted switch-response time behavior.”

Further, it's unclear to me how, or why, the authors changed the specific parameters they used to model the optogenetic manipulation. Were these parameters chosen because they fit the manipulation data? This I don't think is in itself an issue, but perhaps should be clearly stated, because otherwise it sounds a bit odd given the parameter changes are so specific. It is also not clear to me why the noise in the diffusion process would be expected to change with increased inhibition. 

We have clarified that our parameters were chosen to best fit behavior (Line 266):

“The model’s parameters were chosen to fit the distribution of switch-response times:

𝑭 = 𝟏, 𝒃 = 𝟎. 𝟓𝟐 (so 𝑻 = 𝟎. 𝟖𝟕), 𝑫 = 𝟎. 𝟏𝟑𝟓, 𝝈 = 𝟎. 𝟎𝟓𝟐 for intact D2-MSNs (Fig 4A, in black); and  𝑭 = 𝟎, 𝒃 = 𝟎. 𝟒𝟖 (so 𝑻 = 𝟎. 𝟏𝟑), 𝑫 = 𝟎. 𝟏𝟒𝟏, 𝝈 = 𝟎. 𝟎𝟓𝟐 for intact D1-MSNs (Fig 4B, in black).”

Furthermore, we have clarified the approach to noise in the results (Line 247):  

“The drift, together with noise 𝝃(𝒕) (of zero mean and strength 𝝈), leads to fluctuating accumulation which eventually crosses a threshold 𝑻 (see Equation 3; Fig 4A-B).”

And Line 279: 

“The results were obtained by simultaneously decreasing the drift rate D  (equivalent to lengthening the neurons’ integration time constant) and lowering the level of network noise 𝝈: D = 𝟎. 𝟏𝟐𝟗, 𝝈 = 𝟎. 𝟎𝟒𝟑 for D2-MSNs in Fig 4A (in red; changes in noise had to accompany changes in drift rate to preserve switch response time variance); and 𝑫 = 𝟎. 𝟏𝟐𝟐, 𝝈 = 𝟎. 𝟎𝟒𝟑  for D1-MSNs in Fig 4B (in blue). The model predicted that disrupting either D2-MSNs or D1-MSNs would increase switch response times (Fig 4C and Fig 4D) and would shift MSN dynamics.”

Regarding the results in Figure 6: 

My comments regarding the interpretation of PCs in Figure 2 apply here as well. In addition, I am not sure that examining PC2 adds much here, given that the authors didn't examine such nonlinear changes earlier in the paper. 

We agree – we removed PC2 for these reasons. We have also noted that the primary reason for PC1 was to compare results of D2/D1 blockade (Line 362):

“We noticed differences in MSN activity across the interval with D2 blockade and D1 blockade at the individual MSN level (Fig 6B-D) as well as at the population level (Fig 6E). We used PCA to quantify effects of D2 blockade or D1 blockade (Bruce et al., 2021; Emmons et al., 2017; Kim et al., 2017a). We constructed principal components (PC) from z-scored peri-event time histograms of firing rate from saline, D2 blockade, and D1 blockade sessions for all mice together. The first component (PC1), which explained 54% of neuronal variance, exhibited “timedependent ramping”, or monotonic changes over the 6 second interval immediately after trial start (Fig 6F-G; variance for PC1 p = 0.001 vs 46 (45-47)% variance in random data; Narayanan, 2016).”

As noted above, PC1 does not explain this level of variance in noisy data.

We also reworked Figure 6 to make the effects of D2 and D1 blockade more apparent by moving the matched sorting to the main figure: 

A larger concern though that seems potentially at odds with the authors' interpretation is that there seems to be very little change in the firing pattern after D1 or D2 blockade. I see that in Figure 6F the authors suggest that many cells slope down (and thus, presumably, they are recoding more D1 cells), and that this change in slope is decreased, but this effect is not apparent in Figure 6C, and Figure 6B shows an example of a cell that seems to fire in the opposite direction (increase activity). I think it would help to show some (more) individual examples that demonstrate the summary effect shown by the authors, and perhaps the authors can comment on the robustness (or the variability) of this result. 

These are important suggestions, we changed our analysis to better capture the variability and main effects in the data, exactly as the reviewer suggested. First, we now included 3 individual raster examples, exactly as the reviewer suggested

As the reviewer suggested, we wanted to compare variability for *all* MSNs. We sorted the same MSNs across saline, D2 blockade, and D1 blockade sessions. We detailed these sorting details in the methods (Line 618):

“Single-unit recordings were made using a multi-electrode recording system (Open

Ephys, Atlanta, GA). After the experiments, Plexon Offline Sorter (Plexon, Dallas, TX), was used to remove artifacts. Principal component analysis (PCA) and waveform shape were used for spike sorting. Single units were defined as those 1) having a consistent waveform shape, 2) being a separable cluster in PCA space, and 3) having a consistent refractory period of at least 2 milliseconds in interspike interval histograms. The same MSNs were sorted across saline, D2 blockade, and D1 blockade sessions by loading all sessions simultaneously in Offline Sorter and sorted using the preceding criteria. MSNs had to have consistent firing in all sessions to be included. Sorting integrity across sessions was quantified by comparing waveform similarity via correlation coefficients between sessions.”

To confirm that we were able to track neurons across sessions, we quantified waveform similarity (Line 353):

“We analyzed 99 MSNs in sessions with saline, D2 blockade, and D1 blockade. We matched MSNs across sessions based on waveform and interspike intervals; waveforms were highly similar across sessions (correlation coefficient between matched MSN waveforms: saline vs D2 blockade r = 1.00 (0.99 – 1.00 rank sum vs correlations in unmatched waveforms p = 3x10-44; waveforms; saline vs D1 blockade r = 1.00 (1.00 – 1.00), rank sum vs correlations in unmatched waveforms p = 4x10-50). There were no consistent changes in MSN average firing rate with D2 blockade or D1 blockade (F = 1.1, p = 0.30 accounting for variance between MSNs; saline: 5.2 (3.3 – 8.6) Hz; D2 blockade 5.1 (2.7 – 8.0) Hz; F = 2.2, p = 0.14; D1 blockade 4.9 (2.4 – 7.8) Hz).”

As noted above, this enabled us to compare activity for the same MSNs across sessions in a new Figure 6 (previously, this analysis had been in Figure S9), and used PCA to quantify this variability.

By tracking neurons across saline, D2 blockade, and D1 blockade, readers can see all the variability in MSNs. We added these data to the results (Line 362):  

“We noticed differences in MSN activity across the interval with D2 blockade and D1 blockade at the individual MSN level (Fig 6B-D) as well as at the population level (Fig 6E). We used PCA to quantify effects of D2 blockade or D1 blockade (Bruce et al., 2021; Emmons et al., 2017; Kim et al., 2017a). We constructed principal components (PC) from z-scored peri-event time histograms of firing rate from saline, D2 blockade, and D1 blockade sessions for all mice together. The first component (PC1), which explained 54% of neuronal variance, exhibited “timedependent ramping”, or monotonic changes over the 6 second interval immediately after trial start (Fig 6F-G; variance for PC1 p = 0.001 vs 46 (45-47)% variance in random data; Narayanan, 2016). Interestingly, PC1 scores shifted with D2 blockade (Fig 6F; PC1 scores for D2 blockade: -0.6 (-3.8 – 4.7) vs saline: -2.3 (-4.2 – 3.2), F = 5.1, p = 0.03 accounting for variance between MSNs; no reliable effect of sex (F = 0.2, p = 0.63) or switching direction (F = 2.8, p = 0.10)). PC1 scores also shifted with D1 blockade (Fig 6F; PC1 scores for D1 blockade: -0.0 (-3.9 – 4.5), F = 5.8, p = 0.02 accounting for variance between MSNs; no reliable effect of sex (F = 0.0, p = 0.93) or switching direction (F = 0.9, p = 0.34)). There were no reliable differences in PC1 scores between D2 and D1 blockade. Furthermore, PC1 was distinct even when sessions were sorted independently and assumed to be fully statistically independent (Figure S10; D2 blockade vs saline: F = 5.8, p = 0.02; D1 blockade vs saline: F = 4.9, p = 0.03; all analyses accounting for variance between mice). Higher components explained less variance and were not reliably different between saline and D2 blockade or D1 blockade. Taken together, this data-driven analysis shows that D2 and D1 blockade produced similar shifts in MSN population dynamics represented by PC1. When combined with the major contributions of D1/D2 MSNs to PC1 (Fig 3C) these findings indicate that pharmacological D2 blockade and D1 blockade disrupt ramping-related activity in the striatum.”

Finally, we included the data in which sessions were sorted independently and assumed to be fully statistically independent in a new Figure S10.

And in the results (Line 376): 

“Furthermore, PC1 was distinct even when sessions were sorted independently and assumed to be fully statistically independent (Figure S10; D2 blockade vs saline: F = 5.8, p = 0.02; D1 blockade vs saline: F = 4.9, p = 0.03; all analyses accounting for variance between mice). Higher components explained less variance and were not reliably different between saline and D2 blockade or D1 blockade.”

These changes strengthen the manuscript and better show the main effects and variability of the data. 

Regarding the results in Figure 7: 

I am overall a bit confused about what the authors are trying to claim here. In Figure 7, they present data suggesting that D1 or D2 blockade disrupts their ability to decode time in the interval of interest (0-6 seconds). However, in the final paragraph of the results, the authors seem to say that by using another technique, they didn't see any significant change in decoding accuracy after D1 or D2 blockade. What do the authors make of this? 

This was very unclear. The second classifier was predicting response time, but it was confusing, and we removed it. 

Impact: 

The task and data presented by the authors are very intriguing, and there are many groups interested in how striatal activity contributes to the neural perception of time. The authors perform a wide variety of experiments and analysis to examine how DMS activity influences time perception during an interval-timing task, allowing for insight into this process. However, the significance of the key finding - that D2/D1 activity increases/ decreases with time - remains somewhat ambiguous to me. This arises from a lack of clarity regarding the initial hypothesis and the implications of this finding for advancing our understanding of striatal functions. 

As noted above, we clarified our hypothesis and implications, and strengthened several aspects of the data as suggested by this reviewer.  

Reviewer #2 (Public Review): 

Summary: 

In the present study, the authors investigated the neural coding mechanisms for D1- and D2expressing striatal direct and indirect pathway MSNs in interval timing by using multiple strategies. They concluded that D2-MSNs and D1-MSNs have opposing temporal dynamics yet disrupting either type produced similar effects on behavior, indicating the complementary roles of D1- and D2- MSNs in cognitive processing. However, the data was incomplete to fully support this major finding. One major reason is the heterogenetic responses within the D1-or D2MSN populations. In addition, there are additional concerns about the statistical methods used. For example, the majority of the statistical tests are based on the number of neurons, but not the number of mice. It appears that the statistical difference was due to the large sample size they used (n=32 D2-MSNs and n=41 D1-MSNs), but different neurons recorded in the same mouse cannot be treated as independent samples; they should use independent mouse-based statistical analysis. 

Strengths: 

The authors used multiple approaches including awake mice behavior training, optogeneticassistant cell-type specific recording, optogenetic or pharmacological manipulation, neural computation, and modeling to study neuronal coding for interval timing. 

We appreciate the reviewer’s careful read recognizing the breadth of our approach.  

Weaknesses: 

(1) More detailed behavior results should be shown, including the rate of the success switches, and how long it takes to wait in the second nose poke to get a reward. For line 512 and the Figure 1 legend, the reviewer is not clear about the reward delivery. The methods appear to state that the mouse had to wait for 18s, then make nose pokes at the second port to get the reward. What happens if the mouse made the second nose poke before 18 seconds, but then exited? Would the mouse still get the reward at 18 seconds? Similarly, what happens if the mice made the third or more nosepokes within 18 seconds? It is important to clarify because, according to the method described, if the mice made a second nose poke before 18 seconds, this already counted as the mouse making the "switch." Lastly, what if the mice exited before 6s in the first nosepoke? 

We completely agree. We have now completely revised Figure 1 to include many of these task details.

We have clarified remaining details in the methods (Line 548):

“Interval timing switch task. We used a mouse-optimized operant interval timing task described in detail previously (Balci et al., 2008; Bruce et al., 2021; Tosun et al., 2016; Weber et al., 2023). Briefly, mice were trained in sound-attenuating operant chambers, with two front nosepokes flanking either side of a food hopper on the front wall, and a third nosepoke located at the center of the back wall. The chamber was positioned below an 8-kHz, 72-dB speaker (Fig 1A; MedAssociates, St. Albans, VT). Mice were 85% food restricted and motivated with 20 mg sucrose pellets (BioServ, Flemington, NJ). Mice were initially trained to receive rewards during fixed ratio nosepoke response trials. Nosepoke entry and exit were captured by infrared beams. After shaping, mice were trained in the “switch” interval timing task. Mice self-initiated trials at the back nosepoke, after which tone and nosepoke lights were illuminated simultaneously. Cues were identical on all trial types and lasted the entire duration of the trial (6 or 18 seconds). On 50% of trials, mice were rewarded for a nosepoke after 6 seconds at the designated first ‘front’ nosepoke; these trials were not analyzed. On the remaining 50% of trials, mice were rewarded for nosepoking first at the ‘first’ nosepoke location and then switching to the ‘second’ nosepoke location; the reward was delivered for initial nosepokes at the second nosepoke location after 18 seconds when preceded by a nosepoke at the first nosepoke location.  Multiple nosepokes at each nosepokes were allowed. Early responses at the first or second nosepoke were not reinforced. Initial responses at the second nosepoke rather than the first nosepoke, alternating between nosepokes, going back to the first nosepoke after the second nosepoke were rare after initial training. Error trials included trials where animals responded only at the first or second nosepoke and were also not reinforced. We did not analyze error trials as they were often too few to analyze; these were analyzed at length in our prior work (Bruce et al., 2021).

Switch response time was defined as the moment animals departed the first nosepoke before arriving at the second nosepoke. Critically, switch responses are a time-based decision guided by temporal control of action because mice switch nosepokes only if nosepokes at the first location did not receive a reward after 6 seconds. That is, mice estimate if more than 6 seconds have elapsed without receiving a reward to decide to switch responses. Mice learn this task quickly (3-4 weeks), and error trials in which an animal nosepokes in the wrong order or does not nosepoke are relatively rare and discarded. Consequently, we focused on these switch response times as the key metric for temporal control of action. Traversal time was defined as the duration between first nosepoke exit and second nosepoke entry and is distinct from switch response time when animals departed the first nosepoke. Nosepoke duration was defined as the time between first nosepoke entry and exit for the switch response times only. Trials were self-initiated, but there was an intertrial interval with a geometric mean of 30 seconds between trials.”

And in the results on Line 131: 

“We investigated cognitive processing in the striatum using a well-described mouseoptimized interval timing task which requires mice to respond by switching between two nosepokes after a 6-second interval (Fig 1A; see Methods; (Balci et al., 2008; Bruce et al., 2021; Larson et al., 2022; Tosun et al., 2016; Weber et al., 2023)). In this task, mice initiate trials by responding at a back nosepoke, which triggers auditory and visual cues for the duration of the trial. On 50% of trials, mice were rewarded for nosepoking after 6 seconds at the designated ‘first’ front nosepoke; these trials were not analyzed. On the remaining 50% of trials, mice were rewarded for nosepoking at the ‘first’ nosepoke and then switching to the ‘second’ nosepoke; initial nosepokes at the second nosepoke after 18 seconds triggered reward when preceded by a first nosepoke. The first nosepokes occurred before switching responses and the second nosepokes occurred much later in the interval in anticipation of reward delivery at 18 seconds (Fig 1B-D). During the task, movement velocity peaked before 6 seconds as mice traveled to the front nosepoke (Fig 1E).

We focused on the switch response time, defined as the moment mice exited the first nosepoke before entering the second nosepoke. Switch responses are a timebased decision guided by temporal control of action because mice switch nosepokes only if nosepoking at the first nosepokes does not lead to a reward after 6 seconds (Fig 1B-E). Switch responses are guided by internal estimates of time because no external cue indicates when to switch from the first to the second nosepoke (Balci et al., 2008; Bruce et al., 2021; Tosun et al., 2016; Weber et al., 2023). We defined the first 6 seconds after trial start as the ‘interval’, because during this epoch mice are estimating whether 6 seconds have elapsed and if they need to switch responses. In 30 mice, switch response times were 9.3 seconds (8.4 – 9.7; median (IQR)); see Table 1 for a summary of mice, experiments, trials, and sessions). We studied dorsomedial striatal D2-MSNs and D1-MSNs using a combination of optogenetics and neuronal ensemble recordings in 9 transgenic mice (4 D2-Cre mice switch response time 9.7 (7.0 – 10.3) seconds; 5 D1-Cre mice switch response time 8.2 (7.7 – 8.7) seconds; rank sum p = 0.73; Table 1).”

(2) There are a lot of time parameters in this behavior task, the description of those time parameters is mentioned in several parts, in the figure legend, supplementary figure legend, and methods, but was not defined clearly in the main text. It is inconvenient, sometimes, confusing for the readers. The authors should make a schematic diagram to illustrate the major parameters and describe them clearly in the main text. 

We agree. We have clarified this in a new schematic, shading the interval in gray:   

And in the results on line 131:

“We focused on the switch response time, defined as the moment mice exited the first nosepoke before entering the second nosepoke. Switch responses are a time-based decision guided by temporal control of action because mice switch nosepokes only if nosepoking at the first nosepokes does not lead to a reward after 6 seconds (Fig 1BE). Switch responses are guided by internal estimates of time because no external cue indicates when to switch from the first to the second nosepoke (Balci et al., 2008; Bruce et al., 2021; Tosun et al., 2016; Weber et al., 2023). We defined the first 6 seconds after trial start as the ‘interval’, because during this epoch mice are estimating whether 6 seconds have elapsed and if they need to switch responses. In 30 mice, switch response times were 9.3 seconds (8.4 – 9.7; median (IQR)); see Table 1 for a summary of mice, experiments, trials, and sessions). We studied dorsomedial striatal D2-MSNs and D1-MSNs using a combination of optogenetics and neuronal ensemble recordings in 9 transgenic mice (4 D2-Cre mice switch response time 9.7

(7.0 – 10.3) seconds; 5 D1-Cre mice switch response time 8.2 (7.7 – 8.7) seconds; rank sum p = 0.73; Table 1).”

(3) In Line 508, the reviewer suggests the authors pay attention to those trials without "switch". It would be valuable to compare the MSN activity between those trials with or without a "switch". 

This is a great suggestion. We analyzed such error trials and MSN activity in Figure 6 of Bruce et al., 2021. However, this manuscript was not designed to analyze errors, as they are rare beyond initial training (Bruce et al., 2021 focused on early training), and too inconsistent to permit robust analysis. This was added to the methods on Line 567:

“Early responses at the first or second nosepoke were not reinforced. Initial responses at the second nosepoke rather than the first nosepoke, alternating between nosepokes, going back to the first nosepoke after the second nosepoke were rare after initial training. Error trials included trials where animals responded only at the first or second nosepoke and were also not reinforced. We did not analyze error trials as they were often too few to analyze; these were analyzed at length in our prior work (Bruce et al., 2021).”

(4) The definition of interval is not very clear. It appears that the authors used a 6-second interval in analyzing the data in Figure 2 and Figure 3. But from my understanding, the interval should be the time from time "0" to the "switch", when the mice start to exit from the first nose poke. 

We have now defined it explicitly in the schematic: 

Incidentally, this reviewer asked us to analyze a longer epoch – this analysis beautifully justifies our focus on the first 6 seconds (now in Figure S2).

We focus on the first six seconds as there are few nosepokes and switch responses during this epoch; however, we consider the reviewer’s definition and analyze the epoch the reviewer suggests from 0 to the switch in analyses below. 

(5) For Figure 2 C-F, the authors only recorded 32 D2-MSNs in 4 mice, and 41 D1-MSNs in 5 mice. The sample size is too small compared to the sample size usually used in the field. In addition to the small sample size, the single-cell activity exhibited heterogeneity, which created potential issues. 

We are glad the reviewer raised these points. First, our tagging dataset is relatively standard for optogenetic tagging. Second, we now include Cohen’s d for both PC and slope results for all optogenetic tagging analysis, which demonstrate that we have adequate statistical power and medium-to-large effect sizes (Line 186): 

“In line with population averages from Fig 2G&H, D2-MSNs and D1-MSNs had opposite patterns of activity with negative PC1 scores for D2-MSNs and positive PC1 scores for D1-MSNs (Fig 3C; PC1 for D2-MSNs: -3.4 (-4.6 – 2.5); PC1 for D1MSNs: 2.8 (-2.8 – 4.9); F = 8.8, p = 0.004 accounting for variance between mice (Fig S3A); Cohen’s d = 0.7; power = 0.80; no reliable effect of sex (F = 0.44, p = 0.51) or switching direction (F = 1.73, p = 0.19)).”

And Line 197:

“GLM analysis also demonstrated that D2-MSNs had significantly different slopes (0.01 spikes/second (-0.10 – 0.10)), which were distinct from D1-MSNs (-0.20 (-0.47– 0.06; Fig 3D; F = 8.9, p = 0.004 accounting for variance between mice (Fig S3B); Cohen’s d = 0.8; power = 0.98; no reliable effect of sex (F = 0.02, p = 0.88) or switching direction (F = 1.72, p = 0.19)).”

We added boxplots to Figure 3, which better highlight differences in these distributions.

However, the reviewer’s point is well-taken, and we have added a caveat to the discussion exactly as the reviewer suggested (Line 496):

“Second, although we had adequate statistical power and medium-to-large effect sizes, optogenetic tagging is low-yield, and it is possible that recording more of these neurons would afford greater opportunity to identify more robust results and alternative coding schemes, such as neuronal synchrony.”

For both D1 and D2 MSNs, the authors tried to make conclusions on the "trend" of increasing in D2-MSNs and decreasing in D1-MSNs populations, respectively, during the interval. However, such a conclusion is not sufficiently supported by the data presented. It looks like the single-cell activity patterns can be separated into groups: one is a decreasing activity group, one is an increasing activity group and a small group for on and off response. Because of the small sample size, the author should pay attention to the variance across different mice (which needs to be clearly presented in the manuscript), instead of pooling data together and analyzing the mean activity. 

We were not clear – we now do exactly as the reviewer suggested. We are not pooling any data – instead – as we state on line 620 - we are using linear-mixed effects models to account for mouse-specific and neuron-specific variance. This approach was developed with our statistics core for exactly the reasons the reviewer suggested (see letter). We state this explicitly in the methods (Line 704):

“Statistics. All data and statistical approaches were reviewed by the Biostatistics,

Epidemiology, and Research Design Core (BERD) at the Institute for Clinical and Translational Sciences (ICTS) at the University of Iowa. All code and data are made available at http://narayanan.lab.uiowa.edu/article/datasets. We used the median to measure central tendency and the interquartile range to measure spread. We used Wilcoxon nonparametric tests to compare behavior between experimental conditions and Cohen’s d to calculate effect size. Analyses of putative single-unit activity and basic physiological properties were carried out using custom routines for MATLAB.

For all neuronal analyses, variability between animals was accounted for using generalized linear-mixed effects models and incorporating a random effect for each mouse into the model, which allows us to account for inherent between-mouse variability. We used fitglme in MATLAB and verified main effects using lmer in R. We accounted for variability between MSNs in pharmacological datasets in which we could match MSNs between saline, D2 blockade, and D1 blockade. P values < 0.05 were interpreted as significant.”

We have now stated in the results that we are explicitly accounting for variance between mice (Line 186): 

“In line with population averages from Fig 2G&H, D2-MSNs and D1-MSNs had opposite patterns of activity with negative PC1 scores for D2-MSNs and positive PC1 scores for D1-MSNs (Fig 3C; PC1 for D2-MSNs: -3.4 (-4.6 – 2.5); PC1 for D1MSNs: 2.8 (-2.8 – 4.9); F = 8.8, p = 0.004 accounting for variance between mice (Fig S3A); Cohen’s d = 0.7; power = 0.80; no reliable effect of sex (F = 0.44, p = 0.51) or switching direction (F = 1.73, p = 0.19)).”

And on Line 197:

“GLM analysis also demonstrated that D2-MSNs had significantly different slopes (0.01 spikes/second (-0.10 – 0.10)), which were distinct from D1-MSNs (-0.20 (-0.47– 0.06; Fig 3D; F = 8.9, p = 0.004 accounting for variance between mice (Fig S3B); Cohen’s d = 0.8; power = 0.98; no reliable effect of sex (F = 0.02, p = 0.88) or switching direction (F = 1.72, p = 0.19)).”

All statistics in the manuscript now explicitly account for variance between mice. 

This is the approach that was recommended by our the Biostatistics, Epidemiology, and

Research Design Core (BERD) at the Institute for Clinical and Translational Sciences (ICTS) at the University of Iowa, who reviews all of our work.

We note that these Cohen d values usually interpret as medium or large. 

We performed statistical power calculations and include these to aid readers’ interpretation. These are all >0.8. 

Finally, the reviewer uses the word ‘trend’. We define p values <0.05 as significant in the methods, and do not interpret trends (on line 717): 

“P values < 0.05 were interpreted as significant.”

And, we have now plotted values for each mouse in a new Figure S3.

As noted in the figure legend, mouse-specific effects were analyzed using linear models that account for between-mouse variability, as discussed with our statisticians. However, the reviewer’s point is well taken, and we have added this idea to the discussion as suggested (Line 496):

“Second, although we had adequate statistical power and medium-to-large effect sizes, optogenetic tagging is low-yield, and it is possible that recording more of these neurons would afford greater opportunity to identify more robust results and alternative coding schemes, such as neuronal synchrony.”

(6) For Figure 2, from the activity in E and F, it seems that the activity already rose before the trial started, the authors should add some longer baseline data before time zero for clarification and comparison and show the timing of the actual start of the activity with the corresponding behavior. What behavior states are the mice in when initiating the activity? 

This is a key point. First, we are not certain what state the animal is in until they initiate trials at the back nosepoke (“Start”). Therefore, we cannot analyze this epoch.  

However, we can show neuronal activity during a longer epoch exactly as the reviewer suggested. Although there are modulations, the biggest difference between D2 and D1 MSNs is during the 0-6 second interval. This analysis supports our focus on the 0-6 second interval. We have included this as a new Figure S2.

(7) The authors were focused on the "switch " behavior in the task, but they used an arbitrary 6s time window to analyze the activity, and tried to correlate the decreasing or increasing activities of MSNs to the neural coding for time. A better way to analyze is to sort the activity according to the "switch" time, from short to long intervals. This way, the authors could see and analyze whether the activity of D1 or D2 MSNs really codes for the different length of interval, instead of finding a correlation between average activity trends and the arbitrary 6s time window. 

This is a great suggestion. We did exactly this and adjusted our linear models on a trialby-trial basis to account for time between the start of the interval and the switch. This is now added to the methods (line 656): 

“We performed additional sensitivity analysis excluding outliers and measuring firing rate from the start of the interval to the time of the switch response on a trialby-trial level for each neuron.”

And to the results (Line 201):

“We found that D2-MSNs and D1-MSNs had a significantly different slope even when excluding outliers (4 outliers excluded outside of 95% confidence intervals; F=7.51, p=0.008 accounting for variance between mice) and when the interval was defined as the time between trial start and the switch response on a trial-by-trial basis for each neuron (F=4.3, p=0.04 accounting for variance between mice).”

We now state our justification for focusing on the first 6 seconds of the interval (Line 134)

“Switch responses are guided by internal estimates of time and temporal control of action because no external cue indicates when to switch from the first to the second nosepoke (Balci et al., 2008; Bruce et al., 2021; Tosun et al., 2016; Weber et al., 2023). We defined the first 6 seconds after trial start as the ‘interval’, because during this epoch mice are estimating whether 6 seconds have elapsed and if they need to switch responses.”

As noted previously, epoch is now justified by Figure S2E.

And we note that this focus minimizes motor confounds (Line 511):

“Four lines of evidence argue that our findings cannot be directly explained by motor confounds: 1) D2-MSNs and D1-MSNs diverge between 0-6 seconds after trial start well before the first nosepoke (Fig S2), 2) our GLM accounted for nosepokes and nosepoke-related βs were similar between D2-MSNs and D1-MSNs, 3) optogenetic disruption of dorsomedial D2-MSNs and D1-MSNs did not change task-specific movements despite reliable changes in switch response time, and 4) ramping dynamics were quite distinct from movement dynamics. Furthermore, disrupting D2-MSNs and D1-MSNs did not change the number of rewards animals received, implying that these disruptions did not grossly affect motivation. Still, future work combining motion tracking with neuronal ensemble recording and optogenetics and including bisection tasks may further unravel timing vs. movement in MSN dynamics (Robbe, 2023).”

We are glad the reviewer suggested this analysis as it strengthens our manuscript.  

Reviewer #3 (Public Review): 

Summary: 

The cognitive striatum, also known as the dorsomedial striatum, receives input from brain regions involved in high-level cognition and plays a crucial role in processing cognitive information. However, despite its importance, the extent to which different projection pathways of the striatum contribute to this information processing remains unclear. In this paper, Bruce et al. conducted a study using a range of causal and correlational techniques to investigate how these pathways collectively contribute to interval timing in mice. Their results were consistent with previous research, showing that the direct and indirect striatal pathways perform opposing roles in processing elapsed time. Based on their findings, the authors proposed a revised computational model in which two separate accumulators track evidence for elapsed time in opposing directions. These results have significant implications for understanding the neural mechanisms underlying cognitive impairment in neurological and psychiatric disorders, as disruptions in the balance between direct and indirect pathway activity are commonly observed in such conditions. 

Strengths: 

The authors employed a well-established approach to study interval timing and employed optogenetic tagging to observe the behavior of specific cell types in the striatum. Additionally, the authors utilized two complementary techniques to assess the impact of manipulating the activity of these pathways on behavior. Finally, the authors utilized their experimental findings to enhance the theoretical comprehension of interval timing using a computational model. 

We are grateful for the reviewer’s consideration of our work and for recognizing the strengths of our approach.  

Weaknesses: 

The behavioral task used in this study is best suited for investigating elapsed time perception, rather than interval timing. Timing bisection tasks are often employed to study interval timing in humans and animals.

This is a key point, and the reviewer is correct. We use our task because of its’ translational validity; as far as we know, temporal bisection tasks have been used less often in human disease and in rodent models. We have included a new paragraph describing this in the discussion (Line 472):

“Because interval timing is reliably disrupted in human diseases of the striatum such as Huntington’s disease, Parkinson’s disease, and schizophrenia (Hinton et al., 2007; Singh et al., 2021; Ward et al., 2011), these results have relevance to human disease. Our task version has been used extensively to study interval timing in mice and humans (Balci et al., 2008; Bruce et al., 2021; Stutt et al., 2024; Tosun et al., 2016; Weber et al., 2023). However, temporal bisection tasks, in which animals hold during a temporal cue and respond at different locations depending on cue length, have advantages in studying how animals time an interval because animals are not moving while estimating cue duration (Paton and Buonomano, 2018; Robbe, 2023; Soares et al., 2016). Our interval timing task version – in which mice switch between two response nosepokes to indicate their interval estimate has elapsed – has been used extensively in rodent models of neurodegenerative disease (Larson et al., 2022; Weber et al., 2024, 2023; Zhang et al., 2021), as well as in humans (Stutt et al., 2024). Furthermore, because many therapeutics targeting dopamine receptors are used clinically, these findings help describe how dopaminergic drugs might affect cognitive function and dysfunction. Future studies of D2-MSNs and D1-MSNs in temporal bisection and other timing tasks may further clarify the relative roles of D2- and D1-MSNs in interval timing and time estimation.”

Furthermore, we have modified the use of the definition of interval timing in the abstract, introduction, and results to reflect the reviewers comment. For instance, in the abstract (Line 43):

“We studied dorsomedial striatal cognitive processing during interval timing, an elementary cognitive task that requires mice to estimate intervals of several seconds and involves working memory for temporal rules as well as attention to the passage of time.”

However, we think it is important to use the term ‘interval timing’ as it links to past work by our group and others.   

The main results from unit recording (opposing slopes of D1/D2 cell firing rate, as shown in Figure 3D) appear to be very sensitive to a couple of outlier cells, and the predictive power of ensemble recording seems to be only slightly above chance levels. 

This is a key point raised by other reviewers as well. We have now included measures of statistical power (as we interpret the reviewer’s comment of predictive power), effect size, and perform additional sensitivity analyses (Line 187): 

“PC1 scores for D1-MSNs (Fig 3C; PC1 for D2-MSNs: -3.4 (-4.6 – 2.5); PC1 for D1MSNs: 2.8 (-4.9 – -2.8); F=8.8, p = 0.004 accounting for variance between mice (Fig S3A);  Cohen’s d = 0.7; power = 0.80; no reliable effect of sex (F=1.9, p=0.17) or switching direction (F=0.1, p=0.75)).”

And on Line 197:

“GLM analysis also demonstrated that D2-MSNs had significantly different slopes (0.01 spikes/second (-0.10 – 0.10)), which were distinct from D1-MSNs (-0.20 (-0.45– 0.06; Fig 3D; F=8.9, p = 0.004 accounting for variance between mice (Fig S3B); Cohen’s d = 0.8; power = 0.98).  We found that D2-MSNs and D1-MSNs had a significantly different slope even when excluding outliers (4 outliers excluded outside of 95% confidence intervals; F=7.51, p=0.008 accounting for variance between mice) and when the interval was defined as the time between trial start and the switch response on a trial-by-trial basis for each neuron (F=4.3, p=0.04 accounting for variance between mice).”

These are medium-to-large Cohen’s d results, and we have adequate statistical power. These results are not easily explained by chance. 

We also added boxplots, which highlight the differences in distribution.

Finally, we note that our conclusions are drawn from many convergent analyses (on Line 216): 

“Analyses of average activity, PC1, and trial-by-trial firing-rate slopes over the interval provide convergent evidence that D2-MSNs and D1-MSNs had distinct and opposing dynamics during interval timing.”

In the optogenetic experiment, the laser was kept on for too long (18 seconds) at high power (12 mW). This has been shown to cause adverse effects on population activity (for example, through heating the tissue) that are not necessarily related to their function during the task epochs. 

This is an important point. We are well aware of heating effects with optogenetics and other potential confounds. For the exact reasons noted by the reviewer, we had opsinnegative controls – where the laser was on for the exact same amount of time (18 seconds) and at the same power (12 mW)– in Figure S5. We have now better highlighted these controls in the methods (Line 598):

“In animals injected with optogenetic viruses, optical inhibition was delivered via bilateral patch cables for the entire trial duration of 18 seconds via 589-nm laser light at 12 mW power on 50% of randomly assigned trials. We performed control experiments in mice without opsins using identical laser parameters in D2-cre or D1-cre mice (Fig S6).”

And in results (Line 298):

“Importantly, we found no reliable effects for D2-MSNs with opsin-negative controls (Fig S6).”

And Line 306): 

“As with D2-MSNs, we found no reliable effects with opsin-negative controls in D1MSNs (Fig S6).”

We have highlighted these data in Figure S6: 

Furthermore, the effect of optogenetic inhibition is similar to pharmacological effects in this manuscript and in our prior work (De Corte et al., 2019; Stutt et al., 2024) on line 459): 

“Past pharmacological work from our group and others has shown that disrupting D2- or D1-MSNs slows timing (De Corte et al., 2019b; Drew et al., 2007, 2003; Stutt et al., 2024), in line with pharmacological and optogenetic results in this manuscript.”

And in the discussion section on Line 488: 

“Our approach has several limitations. First, systemic drug injections block D2- and D1-receptors in many different brain regions, including the frontal cortex, which is involved in interval timing (Kim et al., 2017a). D2 blockade or D1 blockade may have complex effects, including corticostriatal or network effects that contribute to changes in D2-MSN or D1-MSN ensemble activity. We note that optogenetic inhibition of D2-MSNs and D1-MSNs produces similar effects to pharmacology in Figure 5.”

Given the systemic delivery of pharmacological interventions, it is difficult to conclude that the effects are specific to the dorsomedial striatum. Future studies should use the local infusion of drugs into the dorsomedial striatum. 

This is a great point - we did this experiment in De Corte et al, 2019 with local drug infusions. This earlier study was the departure point for this experiment. We now point this out in the introduction (Line 92): 

“Past work has shown that disrupting either D2-dopamine receptors (D2) or D1dopamine receptors (D1) powerfully impairs interval timing by increasing estimates of elapsed time (Drew et al., 2007; Meck, 2006). Similar behavioral effects were found with systemic (Stutt et al., 2024) or local dorsomedial striatal D2 or D1 disruption (De Corte et al., 2019a). These data lead to the hypothesis that D2 MSNs and D1 MSNs have similar patterns of ramping activity across a temporal interval.”

However, the reviewer makes a great point - and we will develop this in our future work (Line 485): 

“Future studies might extend our work combining local pharmacology with neuronal ensemble recording.”

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Just a few minor notes: 

(1) Figures 2C and D should have error bars. 

We agree.  We added error bars to these figures and other rasters as recommended.  

(2) Figures 2G and H seem to be smoothed - how was this done? 

We added these details.

(3) It is unclear what the 'neural network machine learning classifier' mentioned in lines 193-199 adds if the data relevant to this analysis isn't presented. I would potentially include this. 

We agree. This analysis was confusing and not relevant to our main points; consequently, we removed it.  

Reviewer #2 (Recommendations For The Authors): 

Major: 

(1)  For Figure 2, the description of the main results in (C-F) in the main text is too brief and is not clear. 

We have added to and clarified this text (Line 147)

“Striatal neuronal populations are largely composed of MSNs expressing D2dopamine or D1-dopamine receptors. We optogenetically tagged D2-MSNs and D1MSNs by implanting optrodes in the dorsomedial striatum and conditionally expressing channelrhodopsin (ChR2; Fig S1) in 4 D2-Cre (2 female) and 5 D1-Cre transgenic mice (2 female). This approach expressed ChR2 in D2-MSNs or D1MSNs, respectively (Fig 2A-B; Kim et al., 2017a). We identified D2-MSNs or D1MSNs by their response to brief pulses of 473 nm light; neurons that fired within 5 milliseconds were considered optically tagged putative D2-MSNs (Fig S1B-C). We tagged 32 putative D2-MSNs and 41 putative D1-MSNs in a single recording session during interval timing. There were no consistent differences in overall firing rate between D2-MSNs and D1-MSNs (D2-MSNs: 3.4 (1.4 – 7.2) Hz; D1-MSNs 5.2 (3.1 – 8.6) Hz; F = 2.7, p = 0.11 accounting for variance between mice). Peri-event rasters and histograms from a tagged putative D2-MSN (Fig 2C) and from a tagged putative D1-MSN (Fig 2D) demonstrate prominent modulations for the first 6 seconds of the interval after trial start. Z-scores of average peri-event time histograms (PETHs) from 0 to 6 seconds after trial start for each putative D2-MSN are shown in Fig 2E and for each putative D1-MSN in Fig 2F. These PETHs revealed that for the 6-second interval immediately after trial start, many putative D2-MSN neurons appeared to ramp up while many putative D1-MSNs appeared to ramp down. For 32 putative D2-MSNs average PETH activity increased over the 6second interval immediately after trial start, whereas for 41 putative D1-MSNs, average PETH activity decreased. These differences resulted in distinct activity early in the interval (0-1 seconds; F = 6.0, p = 0.02 accounting for variance between mice), but not late in the interval (5-6 seconds; F = 1.9, p = 0.17 accounting for variance between mice) between D2-MSNs and D1-MSNs. Examination of a longer interval of 10 seconds before to 18 seconds after trial start revealed the greatest separation in D2-MSN and D1-MSN dynamics during the 6-second interval after trial start (Fig S2). Strikingly, these data suggest that D2-MSNs and D1-MSNs might display opposite dynamics during interval timing.”

(2)  For Figure3 

(A)  Is the PC1 calculated from all MSNs of all mice (4 D2, 5 D1 mice)? 

We clarified this (Line 182):

“We analyzed PCA calculated from all D2-MSNs and D1-MSNs PETHs over the 6second interval immediately after trial start.”

And for pharmacology (Line 362): 

“We noticed differences in MSN activity across the interval with D2 blockade and D1 blockade at the individual MSN level (Fig 6B-D) as well as at the population level (Fig 6E). We used PCA to quantify effects of D2 blockade or D1 blockade (Bruce et al., 2021; Emmons et al., 2017; Kim et al., 2017a). We constructed principal components (PC) from z-scored peri-event time histograms of firing rate from saline, D2 blockade, and D1 blockade sessions for all mice together.”

(B)  The authors should perform PCA on single mouse data, and add the plot and error bar. 

This is a great idea. We have now included this as a new Figure S3:   

(C)  As mentioned before, both D2-or D1- MSNs can be divided into three groups, it is not appropriate to put them together as each MSN is not an independent variable, the authors should do the statistics based on the individual mouse, and do the parametric or non-parametric comparison, and plot N (number of mice) based error bars. 

We have done exactly this using a linear mixed effects model, as recommend by our statistics core. They have explicitly suggested that this is the best approach to these data (see letter). We have also included measures of statistical power and effect size (Line 704):  

“All data and statistical approaches were reviewed by the Biostatistics, Epidemiology, and Research Design Core (BERD) at the Institute for Clinical and Translational Sciences (ICTS) at the University of Iowa. All code and data are made available at http://narayanan.lab.uiowa.edu/article/datasets. We used the median to measure central tendency and the interquartile range to measure spread. We used Wilcoxon nonparametric tests to compare behavior between experimental conditions and Cohen’s d to calculate effect size. Analyses of putative single-unit activity and basic physiological properties were carried out using custom routines for MATLAB.

For all neuronal analyses, variability between animals was accounted for using generalized linear-mixed effects models and incorporating a random effect for each mouse into the model, which allows to account for inherent between-mouse variability. We used fitglme in MATLAB and verified main effects using lmer in R. We accounted for variability between MSNs in pharmacological datasets in which we could match MSNs between saline, D2 blockade, and D1 blockade. P values < 0.05 were interpreted as significant.”

We have now included measures of ‘power’ (which we interpret to be statistical), effect size, and perform additional sensitivity analyses (Line 187): 

“PC1 scores for D1-MSNs (Fig 3C; PC1 for D2-MSNs: -3.4 (-4.6 – 2.5); PC1 for D1MSNs: 2.8 (-4.9 – -2.8); F=8.8, p = 0.004 accounting for variance between mice (Fig S3A); Cohen’s d = 0.7; power = 0.80; no reliable effect of sex (F=1.9, p=0.17) or switching direction (F=0.1, p=0.75)).”

And Line 197:

“GLM analysis also demonstrated that D2-MSNs had significantly different slopes (0.01 spikes/second (-0.10 – 0.10)), which were distinct from D1-MSNs (-0.20 (-0.45– 0.06; Fig 3D; F=8.9, p = 0.004 accounting for variance between mice (Fig S3B); Cohen’s d = 0.8; power = 0.98).  We found that D2-MSNs and D1-MSNs had a significantly different slope even when excluding outliers (4 outliers excluded outside of 95% confidence intervals; F=7.51, p=0.008 accounting for variance between mice) and when the interval was defined as the time between trial start and the switch response on a trial-by-trial bases for each neuron (F=4.3, p=0.04 accounting for variance between mice).”

These are medium-to-large Cohen’s d results, and we have adequate statistical power. These results are not easily explained by chance. 

We also added boxplots, which highlight the differences in distributions.

(3) For results in Figure 5 and Figure S7, according to Figure 1 legend, lines 4 to 5, the response times were defined as the moment mice exit the first nose poke (on the left) to respond at the second nose poke; and according to method session (line 522), "switch" traversal time was defined as the duration between first nose poke exit and second nose poke entry. It seems that response time is the switch traversal time, they should be the same, but in Figures B and D, the response time showed a clear difference between the laser off and on groups, while in Figures S7 C, and G, there were no differences between laser off and on group for switch traversal time. Please reconcile these inconsistencies. 

We were not clear. We now clarify – switch responses are the moment when mice depart the first nosepoke, whereas traversal time is the time between departing the first nosepoke and arriving at the second nosepoke. We have reworked our figures to make this clear.

And in the methods (Line 570):

“Switch response time was defined as the moment animals departed the first nosepoke before arriving at the second nosepoke. Critically, switch responses are a time-based decision guided by temporal control of action because mice switch nosepokes only if nosepokes at the first location did not receive a reward after 6 seconds. That is, mice estimate if more than 6 seconds have elapsed without receiving a reward to decide to switch responses. Mice learn this task quickly (3-4 weeks), and error trials in which an animal nosepokes in the wrong order or does not nosepoke are relatively rare and discarded. Consequently, we focused on these switch response times as the key metric for temporal control of action. Traversal time was defined as the duration between first nosepoke exit and second nosepoke entry and is distinct from switch response time when animals departed the first nosepoke. Nosepoke duration was defined as the time between first nosepoke entry and exit for the switch response times only. Trials were self-initiated, but there was an intertrial interval with a geometric mean of 30 seconds between trials.”

And in Figure S8, we have added graphics and clarified the legend.

(4) The first nose poke and second nose poke are very close, why did it take so long to move from the first nose poke to the second nose poke, even though the mouse already made the decision to switch? Please see Figure S1A, it took less than 6s from the back nose poke to the first nose poke, but it took more than 6s (up to 12s) from the first nose poke to the second nose poke, what were the mice's behavior during this period? 

This is a key detail. There is no temporal urgency as only the initial nosepoke after 18 seconds leads to reward. In other words, making a second nosepoke prior to 18 seconds is not rewarded and, in well-trained animals, is wasted effort. We have added these details to the methods (Line 124):

“On the remaining 50% of trials, mice were rewarded for nosepoking at the ‘first’ nosepoke and then switching to the ‘second’ nosepoke; initial nosepokes at the second nosepoke after 18 seconds triggered reward when preceded by a first nosepoke. The first nosepokes occurred before switching responses and the second nosepokes occurred much later in the interval in anticipation of reward delivery at 18 seconds (Fig 1B-D). During the task, movement velocity peaked before 6 seconds as mice traveled to the front nosepoke (Fig 1E).”

And in Figure 1, as described in detail above. 

(5) How many trials did mice perform in one day? How many recordings/day for how many days were performed? 

These are key details that we have now added to Table 1.

We have added the number of recording sessions to the methods (Line 603): 

“For optogenetic tagging, putative D1- and D2-MSNs were optically identified via 473-nm photostimulation. Units with mean post-stimulation spike latencies of ≤5 milliseconds and a stimulated-to-unstimulated waveform correlation ratio of >0.9 were classified as putative D2-MSNs or D1-MSNs (Ryan et al., 2018; Shin et al., 2018). Only one recording session was performed for each animal per day, and one recording session was included from each animal.”

And Line 606: 

“Only one recording session was performed for each animal per day, and one recording session was included from saline, D2 blockade, and D1 blockade sessions.”

(6) For results in Figure 5, the authors should analyze the speed for the laser on and off group, since the dorsomedial striatum was reported to be related to control of speed (Yttri, Eric A., and Joshua T. Dudman. "Opponent and bidirectional control of movement velocity in the basal ganglia." Nature 533.7603 (2016): 402-406.). 

We have some initial DeepLabCut data and have included it in a new Figure 1E.

B) DeepLabCut tracking of position during the interval timing revealed that mice moved quickly after trial start and then velocity was relatively constant throughout the trial

We measure movement speed using nosepoke duration and traversal time, which can give some measure of movement velocity.

In Yttri and Dudman, the mice are head-fixed and moving a joystick, whereas our mice are freely moving. However, we have now included the lack of motor control as a major limitation (Line 510): 

“Finally, movement and motivation contribute to MSN dynamics (Robbe, 2023). Four lines of evidence argue that our findings cannot be directly explained by motor confounds: 1) D2-MSNs and D1-MSNs diverge between 0-6 seconds after trial start well before the first nosepoke (Fig S2), 2) our GLM accounted for nosepokes and nosepoke-related βs were similar between D2-MSNs and D1-MSNs, 3) optogenetic disruption of dorsomedial D2-MSNs and D1-MSNs did not change task-specific movements despite reliable changes in switch response time, and 4) ramping dynamics were quite distinct from movement dynamics. Furthermore, disrupting D2-MSNs and D1-MSNs did not change the number of rewards animals received, implying that these disruptions did not grossly affect motivation. Still, future work combining motion tracking with neuronal ensemble recording and optogenetics and including bisection tasks may further unravel timing vs. movement in MSN dynamics (Robbe, 2023).”

(7)  Figure S3 (C, E, and F), statistics should be done based on N (number of mice), not on the number of recorded neurons.  

We have removed this section, and all other statistics in the paper properly account for mouse-specific variance, as noted above.

(8)  Figure S1 

(A) Are these the results from all mice superposed together, or from one mouse on one given day? How many of the trials' data were superposed?

We included these details in a new Figure 1.

(B, C) How many trials were included? 

(D) How many days did these data cover? 

We have included a new Table 1 with these important details.

We have noted that only 1 recording session / mouse was included in analysis (Line 606):

“Only one recording session was performed for each animal per day, and one recording session was included from each animal.”

And Line 614: 

“Only one recording session was performed for each animal per day, and one recording session was included from saline, D2 blockade, and D1 blockade sessions.”

(9) Figure S2 

(A) Can the authors add coordinates of the brain according to the mouse brain atlas or, alternatively, show it using a coronal section? 

Great idea – added to Figure S2 legend: 

“Figure S1: A) Recording locations in the dorsomedial striatum (targeting AP +0.4, ML -1.4, DV -2.7). Electrode reconstructions for D2-Cre (red), D1-Cre (blue), and wild-type mice (green). Only the left striatum was implanted with electrodes in all animals.”

We have also added it to Figure S5 legend: 

“Figure S5: Fiber optic locations from A) an opsin-expressing mouse with mCherrytagged halorhodopsin and bilateral fiber optics, and B) across 10 D2-Cre mice (red) and 6 D1-cre mice (blue) with fiber optics (targeting AP +0.9, ML +/-1.3, DV –2.5).”

(C) Why did the waveform of laser and no laser seem the same? 

The optogenetically tagged spike waveforms are highly similar, indicating that optogenetically-triggered spikes are like other spikes. That is the main point – optogenetically stimulating the neuron does not change the waveform. We have added this detail to the legend of S1: 

“Inset on bottom right – waveforms from laser trials (red) and trials without laser (blue).  Across 73 tagged neurons, waveform correlation coefficients for laser trials vs. trials without laser was r = 0.97 (0.92-0.99). These data demonstrate that optogenetically triggered spikes are similar to non-optogenetically triggered spikes.”

(10)  Figure S7, what was the laser power used in this experiment? Have the authors tried different laser powers? 

We have now clarified the laser power on line 598: 

“In animals injected with optogenetic viruses, optical inhibition was delivered via bilateral patch cables for the entire trial duration of 18 seconds via 589-nm laser light at 12 mW power on 50% of randomly assigned trials.”

And for Figure S6 (was S7 previously): 

We did not try other laser powers; our parameters were chosen a priori based on our past work.  

(11)  In Figure S9, what method was used to sort the neurons? 

We now clarify in the methods (Line 617): 

“Electrophysiology. Single-unit recordings were made using a multi-electrode recording system (Open Ephys, Atlanta, GA). After the experiments, Plexon Offline Sorter (Plexon, Dallas, TX), was used to remove artifacts. Principal component analysis (PCA) and waveform shape were used for spike sorting. Single units were defined as those 1) having a consistent waveform shape, 2) being a separable cluster in PCA space, and 3) having a consistent refractory period of at least 2 milliseconds in interspike interval histograms.  The same MSNs were sorted across saline, D2 blockade, and D1 blockade sessions by loading all sessions simultaneously in Offline Sorter and sorted using the preceding criteria. MSNs had to have consistent firing in all sessions to be included. Sorting integrity across sessions was quantified by comparing waveform similarity via R2 between sessions.”

And in the results (Line 353):

“We analyzed 99 MSNs in sessions with saline, D2 blockade, and D1 blockade. We matched MSNs across sessions based on waveform and interspike intervals; waveforms were highly similar across sessions (correlation coefficient between matched MSN waveforms: saline vs D2 blockade r = 1.00 (0.99 – 1.00 rank sum vs correlations in unmatched waveforms p = 3x10-44; waveforms; saline vs D1 blockade r = 1.00 (1.00 – 1.00), rank sum vs correlations in unmatched waveforms p = 4x10-50). There were no consistent changes in MSN average firing rate with D2 blockade or D1 blockade (F = 1.1, p = 0.30 accounting for variance between MSNs; saline: 5.2 (3.3 – 8.6) Hz; D2 blockade 5.1 (2.7 – 8.0) Hz; F = 2.2, p = 0.14; D1 blockade 4.9 (2.4 – 7.8) Hz).”

(C-F) statistics should be done based on the number of mice, not on the number of recorded neurons. 

We agree, all experiments are now quantified using linear mixed effects models which formally accounts for variance contributed across animals, as discussed at length earlier in the review and with statistical experts at the University of Iowa.

(12) For results in Figure 6, did the authors do cell-type specific recording on D1 or D2 MSNs using optogenetic tagging? As the D1- or D2- MSNs account for ~50% of all MSNs, the inhibition of a considerable amount of neurons was not observed. The authors should discuss the relation between the results from optogenetic inhibition of D1- or D2- MSNs and pharmacological disruption of D1 or D2 dopamine receptors. 

This is a great point. First, we did not combine cell-type specific recordings with tagging as it was difficult to get enough trials for analysis in a single session in the tagging experiments, and pharmacological interventions can further decrease performance.  However, we have made our results in Figure 6 much more focused.

We have discussed the relationship between these data in the results (Line 380): 

“This data-driven analysis shows that D2 and D1 blockade produced similar shifts in MSN population dynamics represented by PC1.  When combined with major contributions of D1/D2 MSNs to PC1 (Fig 3C) these findings show that pharmacologically disrupting D2 or D1 MSNs can disrupt ramping-related activity in the striatum.”

And in the discussion (Line 417): 

“Strikingly, optogenetic tagging showed that D2-MSNs and D1-MSNs had distinct dynamics during interval timing. MSN dynamics helped construct and constrain a four-parameter drift-diffusion model in which D2- and D1-MSN spiking accumulated temporal evidence. This model predicted that disrupting either D2MSNs or D1-MSNs would increase response times. Accordingly, we found that optogenetically or pharmacologically disrupting striatal D2-MSNs or D1-MSNs increased response times without affecting task-specific movements. Disrupting D2MSNs or D1-MSNs shifted MSN temporal dynamics and degraded MSN temporal encoding. These data, when combined with our model predictions, demonstrate that D2-MSNs and D1-MSNs contribute temporal evidence to controlling actions in time.”

And: 

“D2-MSNs and D1-MSNs play complementary roles in movement. For instance, stimulating D1-MSNs facilitates movement, whereas stimulating D2-MSNs impairs movement (Kravitz et al., 2010). Both populations have been shown to have complementary patterns of activity during movements (Tecuapetla et al., 2016), with MSNs firing at different phases of action initiation and selection. Further dissection of action selection programs reveals that opposing patterns of activation among D2MSNs and D1-MSNs suppress and guide actions, respectively, in the dorsolateral striatum (Cruz et al., 2022). A particular advantage of interval timing is that it captures a cognitive behavior within a single dimension — time. When projected along the temporal dimension, it was surprising that D2-MSNs and D1-MSNs had opposing patterns of activity. Past pharmacological work from our group and others have shown that disrupting D2 or D1 MSNs slows timing (De Corte et al., 2019; Drew et al., 2007, 2003; Stutt et al., 2023), in line with pharmacological and optogenetic results in this manuscript. Computational modeling predicted that disrupting either D2-MSNs or D1-MSNs increased self-reported estimates of time, which was supported by both optogenetic and pharmacological experiments. Notably, these disruptions are distinct from increased timing variability reported with administrations of amphetamine, ventral tegmental area dopamine neuron lesions, and rodent models of neurodegenerative disease (Balci et al., 2008; Gür et al., 2020, 2019; Larson et al., 2022; Weber et al., 2023). Furthermore, our current data demonstrate that disrupting either D2-MSN or D1-MSN activity shifted MSN dynamics and degraded temporal encoding, supporting prior work (De Corte et al., 2019; Drew et al., 2007, 2003; Stutt et al., 2023). Our recording experiments do not identify where a possible response threshold T is instantiated, but downstream basal ganglia structures may have a key role in setting response thresholds (Toda et al., 2017).”

(13) For Figure 2, what is the error region for G and H? Is there a statistically significant difference between the start (e.g., 0-1 s) and the end (e.g., 5-6 s) time? 

G and H are standard error, which we have now clarified.

And on Line 166: 

“These differences resulted in distinct activity early in the interval (0-1 seconds; F = 6.0, p = 0.02 accounting for variance between mice), but not late in the interval (5-6 seconds; F = 1.9, p = 0.17 accounting for variance between mice) between D2-MSNs and D1-MSNs.”

Minor: 

(1)  Figure 2 legend showed the wrong label "Peri-event raster C) from a D2-MSN (red) and E) from a D1-MSN (blue). It should be (D). 

Fixed, thank you.  

(2)  Figure 2. Missing legend for (E) and (F).  

Fixed, thank you.  

(3)  Line 423: mistyped "\" 

Fixed, thank you.  

Reviewer #3 (Recommendations For The Authors): 

-  To clarify that complementary means opposing in this context, I suggest changing the title. 

This is a helpful suggestion. We have changed it exactly as the reviewer suggested: 

“Complementary opposing D2-MSNs and D1-MSNs dynamics during interval timing”

-  I recommend adding a supplementary figure to demonstrate all the nose pokes in all trials in a given session. The current figures make it hard to assess the specifics of the behavior. For example, what happens if, in a long-interval trial, the mouse pokes in the second nose poke before 6 seconds? Is that behavior punished? Do they keep alternating between the nose poke or do they stick to one nose poke? 

We agree. We think this is a main point, and we have now redesigned Figure 1 to describe these details: 

And added these details to the methods (Line 548): 

“Interval timing switch task. We used a mouse-optimized operant interval timing task described in detail previously (Balci et al., 2008; Bruce et al., 2021; Tosun et al., 2016; Weber et al., 2023). Briefly, mice were trained in sound-attenuating operant chambers, with two front nosepokes flanking either side of a food hopper on the front wall, and a third nosepoke located at the center of the back wall. The chamber was positioned below an 8-kHz, 72-dB speaker (Fig 1A; MedAssociates, St. Albans, VT). Mice were 85% food restricted and motivated with 20 mg sucrose pellets (BioServ, Flemington, NJ). Mice were initially trained to receive rewards during fixed ratio nosepoke response trials. Nosepoke entry and exit were captured by infrared beams. After shaping, mice were trained in the “switch” interval timing task. Mice self-initiated trials at the back nosepoke, after which tone and nosepoke lights were illuminated simultaneously. Cues were identical on all trial types and lasted the entire duration of the trial (6 or 18 seconds). On 50% of trials, mice were rewarded for a nosepoke after 6 seconds at the designated first ‘front’ nosepoke; these trials were not analyzed. On the remaining 50% of trials, mice were rewarded for nosepoking first at the ‘first’ nosepoke location and then switching to the ‘second’ nosepoke location; the reward was delivered for initial nosepokes at the second nosepoke location after 18 seconds when preceded by a nosepoke at the first nosepoke location.  Multiple nosepokes at each nosepokes were allowed. Early responses at the first or second nosepoke were not reinforced. Initial responses at the second nosepoke rather than the first nosepoke, alternating between nosepokes, going back to the first nosepoke after the second nosepoke were rare after initial training. Error trials included trials where animals responded only at the first or second nosepoke and were also not reinforced. We did not analyze error trials as they were often too few to analyze; these were analyzed at length in our prior work (Bruce et al., 2021).”

-  Figures 2E and 2F suggest that some D1 cells ramp up during the first 6 seconds, while others ramp down. The same is more or less true for D2s. I wonder if the analysis will lose its significance if the two outlier D1s are excluded from Figure 3D. 

This is a great idea suggested by multiple reviewers. We repeated this analysis with outliers removed. We used a data-driven approach to remove outliers (Line 656): 

“We performed additional sensitivity analysis excluding outliers outside of 95% confidence intervals and measuring firing rate from the start of the interval to the time of the switch response on a trial-by-trial level for each neuron.”

And described these data in the results (Line 201): 

“We found that D2-MSNs and D1-MSNs had a significantly different slope even when excluding outliers (4 outliers excluded outside of 95% confidence intervals; F=7.51, p=0.008 accounting for variance between mice) and when the interval was defined as the time between trial start and the switch response on a trial-by-trial basis for each neuron (F=4.3, p=0.04 accounting for variance between mice).”

Finally, we removed the outliers the reviewers alluded to – two D1 MSNs – and found similar results (F=6.59, p=0.01 for main effect of D2 vs. D1 MSNs controlling for between-mouse variability). We elected to include the more data driven approach based on 95% confidence intervals.

Author response:

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

eLife assessment

This useful manuscript reports mechanisms behind the increase in fecundity in response to sub-lethal doses of pesticides in the crop pest, the brown plant hopper. The authors hypothesize that the pesticide works by inducing the JH titer, which through the JH signaling pathway induces egg development. Evidence for this is, however, inadequate.

We greatly appreciate your valuable comments and constructive suggestions for our work. All in all, the manuscript has been carefully edited and improved following your suggestions. We also provide more evidence to support our statements by conducting new experiments. First, we found that also EB treatment of adult females can stimulate egg-laying. Second, EB treatment in female adults increases the number of mature eggs in the ovary and ovarioles. Third, EB treatment in females enhances the expression of the kr-h1 gene in the whole body of BPH. Finally, EB treatment in female adults increases the JHIII titer, but has no impact on the 20E titer.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Gao et al. have demonstrated that the pesticide emamectin benzoate (EB) treatment of brown planthopper (BPH) leads to increased egg-laying in the insect, which is a common agricultural pest. The authors hypothesize that EB upregulates JH titer resulting in increased fecundity.

Strengths:

The finding that a class of pesticide increases the fecundity of brown planthopper is interesting.

We greatly appreciate your positive comments on our work.

Weaknesses:

(1) EB is an allosteric modulator of GluCl. That means EB physically interacts with GluCl initiating a structural change in the cannel protein. Yet the authors' central hypothesis here is about how EB can upregulate the mRNA of GluCl. I do not know whether there is any evidence that an allosteric modulator can function as a transcriptional activator for the same receptor protein. The basic premise of the paper sounds counterintuitive. This is a structural problem and should be addressed by the authors by giving sufficient evidence about such demonstrated mechanisms before.

Thank you for your question. As the reviewer points out, EB physically interacts with its target protein GluCl and thus affects its downstream signaling pathway. In the manuscript, we reported that EB-treated brown planthoppers display increased expression of GluCl in the adult stage (Fig. 5A). Actually, there are many studies showing that insects treated with insecticides can increase the expression of target genes. For example, the relative expression level of the ryanodine receptor gene of the rice stem borer, Chilo suppressalis was increased 10-fold after treatment with chlorantraniliprole, an insecticide which targets the ryanodine receptor (Peng et al., 2017). Besides this, in Drosophila, starvation (and low insulin) elevates the transcription level of the sNPF and tachykinin receptors (Ko et al., 2015; Root et al., 2011). In brown planthoppers, reduction in mRNA and protein expression of a nicotinic acetylcholine receptor α8 subunit is associated with resistance to imidacloprid (Zhang et al., 2015). RNA interference knockdown of α8 gene decreased the sensitivity of N. lugens to imidacloprid (Zhang et al., 2015). Hence, expression of receptor genes can be regulated by diverse factors including insecticide treatment. In our case, we found that EB can upregulate its target gene GluCl. However, we did not claim that EB functions as transcriptional activator for GluCl, and we still do not know why EB treatment changes the expression of GluCl in the brown planthopper. Considering our experiments are lasting several days, it might be an indirect (or secondary) effect caused by other factors, which change the expression of GluCl gene upon EB action of the channel. One reason is maybe that the allosteric interaction with GluCl by EB makes it dysfunctional and the cellular response is to upregulate the channel/receptor to compensate. We have inserted text on lines 738 - 757 to explain these possibilities.

(2) I am surprised to see a 4th instar larval application or treatment with EB results in the upregulation of JH in the adult stages. Complicating the results further is the observation that a 4th instar EB application results in an immediate decrease in JH titer. There is a high possibility that this late JH titer increase is an indirect effect.

Thank you for your question. Treatment with low doses or sublethal doses of insecticides might have a strong and complex impact on insects (Gandara et al., 2024; Gong et al., 2022; Li et al., 2023; Martelli et al., 2022). We kept the 4th instar of brown planthoppers feeding on EB for four days. They will develop to 5th instar after four days treatment, which is the final nymphal stage of BPH. Since the brown planthopper is a hemimetabolous insect, we cannot rule out the possibility that an indirect effect of treatment with EB results in the upregulation of JH in the adult stages. In this new revised manuscript, we investigated the impact of EB treatment in the adult stage. We found that female adults treated with EB also laid more eggs than controls (Figure 1-figure supplement 1A). The following experiments were performed in adults to address how EB treated stimulates egg-laying in adult brown planthopper.

(1) We found that EB treatment in adults increases the number of mature eggs in ovary (new Figure 2-figure supplement 1). We add this results in lines 234 – 238 and 281-285.

(2) We measured the JH titer after the female adults had been treated with EB. We found that EB can also increase the JH titer but has no impact on the 20E titer in the female adult (Figure 3-S3A and B). We add this results in lines 351 – 356 and 281-285.

(3) EB treatment in adults increases the gene expression of JHAMT and Kr-h1 (Figure 3-S3C and D). We add this results in lines 378 – 379, lines 387-390 and lines 457-462.

(3) The writing quality of the paper needs improvement. Particularly with respect to describing processes and abbreviations. In several instances the authors have not adequately described the processes they have introduced, thus confusing readers.

Thank you for your suggestion. We have thoroughly revised the paper to improve clarity.

(4) In the section 'EB promotes ovarian development' the authors have shown that EB treatment results in increased detention of eggs which contradicts their own results which show that EB promotes egg laying. Again, this is a serious contradiction that nullifies their hypothesis.

Thank you for pointing this out. We revised the figure 2B to show number of mature eggs in the ovary. The number of mature eggs in ovaries of females that fed on EB was higher than in control females. We also show that BPH fed with EB laid more eggs than controls. Thus, our results suggest that EB promotes ovary maturation (and egg production) and also increases egg laying (Figure 1 and Table S1). Thus, we found that EB treatment can increase both the production of eggs and increase egg laying. We add this results in lines 234 – 238.

(5) Furthermore, the results suggest that oogenesis is not affected by EB application. The authors should devote a section to discussing how they are observing increased egg numbers in EB-treated insects while not impacting Oogenesis.

Thank you for your suggestions, and apologies for the lack of clarity in our initial explanation. First, we found that EB treatment led to an increase in the number of eggs laid by female brown planthoppers (Figure 1). Through dissection experiments, we observed that EB-treated females had more mature eggs in their ovaries (Figure 2A and B), indicating that the increased egg-laying was due to a larger production of mature eggs in the ovaries after EB treatment. This is now explained on lines 229-238.

Additionally, since there is no systematic description of oogenesis in the brown planthopper, we were the first to observe the oogenesis process in this species using immunohistochemistry and laser confocal microscopy. Based on the developmental characteristics, we defined the different stages of oogenesis (Figure 2C, Figure 2-figure supplement 2). We did not observe any significant effect of EB treatment on the various stages of oogenesis, indicating that EB treatment does not impair normal egg development (Figure 2D). Instead, the increase in vitellogenin accelerates the production of mature eggs. This is now explained on lines 243-262.

During the maturation process, eggs require uptake of vitellogenin, and an increase in vitellogenin (Vg) content can accelerate egg maturation, producing more mature eggs. Our molecular data suggest that EB treatment leads to an upregulation of vg expression. Based on these findings, we conclude that the increase in egg-laying caused by EB treatment is due to the upregulation of vg (Figure 3I), which raises vitellogenin content, promoting the uptake of vitellogenin by maturing eggs and resulting in the production of more mature eggs. We have revised the text on lines 389-395 to clarify this point.

(6) Met is the receptor of JH and to my understanding, remains mostly constant in terms of its mRNA or protein levels throughout various developmental periods in many different insects. Therefore, the presence of JH becomes the major driving factor for physiological events and not the presence of the receptor Met. Here the authors have demonstrated an increase in Met mRNA as a result of EB treatment. Their central hypothesis is that EB increases JH titer to result in enhanced fecundity. JH action will not result in the activation of Met. Although not contradictory to the hypothesis, the increase in mRNA content of Met is contrary to the findings of the JH field thus far.

Thank you for your comment. Our results showed that EB treatment can mildly increase (about 2-fold) expression of the Met gene in brown planthoppers (Figure 3G). And our data indicated that Met and FAMeT expression levels were not influenced so much by EB compared with kr-h1 and vg (Figure 3H and I). We agree that JH action will not result in the increase of Met. However, we cannot rule out the possibility of other factors (indirect effects), induced by EB treatment that increase the mRNA expression level of Met. One recent paper reported that downregulation of transcription factor CncC will increase met expression in beetles (see Figure 6A in this reference) (Jiang et al., 2023). Many studies have reported that insecticide treatment will activate the CncC gene signaling pathway, which regulates detoxification gene expression (Amezian et al., 2023; Fu et al., 2024; Hu et al., 2021). Hence, it is possible that EB might influence the CncC gene pathway which then induces met expression. This EB effect on met upregulation may be similar to the upregulation of GluCl and some other secondary effects. We have discussed this on lines 725-738.

(7) As pointed out before, it is hard to rationalize how a 4th instar exposure to EB can result in the upregulation of key genes involved in JH synthesis at the adult stage. The authors must consider providing a plausible explanation and discussion in this regard.

Thank you for your comments. It must be mentioned that although we exposed the BPH to EB at 4th instar, we make the insect feed on the EB-treated rice plants for four days. After that, the insect will develop into 5^th instar, the final nymphal stage of brown planthopper. Since brown planthoppers do not have a pupal stage, this might cause the EB presented to the insects last a longer time even in the adult stage. Besides this, we found that EB treatment will increase the weight of adult females (Figure 1-figure supplement 3E and F), which indicates that EB might increase food intake in BPHs that might produce more insulin peptide. Insulin might increase the JH synthesis at the adult stage. In our revised study we also investigate EB impairment in adult BPHs. We found that, similar to the nymphal stage, EB treatment in adult BPHs also increases the egg laying. Furthermore, the JH titer was increased after treatment of BPH with EB in adults. Besides this, GluCl and kr-h1 genes were also up-regulated after EB treatment in the adult stage. We have discussed this on lines 739-746.

(8) I have strong reservations against such an irrational hypothesis that Met (the receptor for JH) and JH-Met target gene Kr-h1 regulate JH titer (Line 311, Fig 3 supplemental 2D). This would be the first report of such an event on the JH field and therefore must be analysed in depth. I strongly suggest the authors remove such claims from the manuscript without substantiating it.

Thank you for your suggestions and comments. We have changed our claims in this revised MS. We found that EB treatment can enhance Kr-h1 expression. We have no evidence to support that JH can induce met expression. We have rewritten the manuscript to avoid confusion (see text on lines 725-735).

(9) Kr-h1 is JH/Met target gene. The authors demonstrate that silencing of Kr-h1 results in inhibition of FAMeT, which is a gene involved in JH synthesis. A feedback loop in JH synthesis is unreported. It is the view of this reviewer that the authors must go ahead with a mechanistic detail of Kr-h1 mediated JH upregulation before this can be concluded. Mere qPCR experiments are not sufficient to substantiate a claim that is completely contrary to the current understanding of the JH signalling pathway.

Thank you for your suggestions and comments. We agree that only qPCR experiments are not enough to provide this kind of claim. More evidences need to be provided to support this. We have revised the MS to avoid confusion (see text on lines 725-735).

(10) The authors have performed knockdowns of JHAMT, Met, and Kr-h1 to demonstrate the effect of these factors on fecundity in BPH. Additionally, they have performed rescue experiments with EB application on these knockdown insects (Figure 3K-M). This, I believe, is a very flawed experiment. The authors demonstrate EB works through JHAMT in upregulating JH titer. In the absence of JHAMT, EB application is not expected to rescue the phenotype. But the authors have reported a complete rescue here. In the absence of Met, the receptor of JH, either EB or JH is not expected to rescue the phenotype. But a complete rescue has been reported. These two experimental results contradict their own hypothesis.

Thank you for your comments. We thought that this rescue is possible since knockdown of the genes is incomplete when using dsRNA injection (and residual gene expression allows for EB action). It is not a total knockout and actually, these genes still have a low level of expression in the dsRNA-injected insects. Since EB can upregulate the expression of JHAMT, Met, and Kr-h1, it is reasonable that EB treatment can rescue the down-regulation effects of these three genes and make fecundity completely rescued. We have clarified this on lines 411-413).

(11) A significant section of the paper deals with how EB upregulates JH titer. JH is a hormone synthesized in the Corpora Allata. Yet the authors have chosen to use the whole body for all of their experiment. Changes in the whole body for mRNA of those enzymes involved in JH synthesis may not reflect the situation in Corpora Allata. Although working with Corpora Allata is challenging, discarding the abdomen and thorax region and working with the head and neck region of the insect is easily doable. Results from such sampling are always more convincing when it comes to JH synthesis studies.

Thank you for your suggestions. Because the head is very difficult to separate from the thorax region in brown planthoppers as you can see in Author response image 1. We are now trying to answer how EB regulates JH synthesis using Drosophila as a model.

Author response image 1.

The brown planthopper

(12) The phenomenon reported was specific to BPH and not found in other insects. This limits the implications of the study.

Thank you for your comments. The brown planthopper is a serious insect pest on rice in Asia. Our findings can guide the use of this insecticide in the field. Besides this, our findings indicated that EB, which targets GluCl can impair the JH titer. Our findings added new implications for how a neuronal system influences the JH signaling pathway. We will further investigate how EB influences JH in the future and will use Drosophila as a model to study the molecular mechanisms.

(13) Overall, the molecular experiments are very poorly designed and can at best be termed superficial. There are several contradictions within the paper and no discussion or explanation has been provided for that.

Thank you for your comments. We have revised the paper according to your suggestions and added further explanation of our results in the discussion parts and hope the conclusions are better supported in the new version. We have discussed this on lines 725-746 and 778-799.

Reviewer #2 (Public Review):

The brown plant hopper (BPH) is a notorious crop pest and pesticides are the most widespread means of controlling its population. This manuscript shows that in response to sublethal doses of the pesticide (EB), BPH females show enhanced fecundity. This is in keeping with field reports of population resurgence post-pesticide treatment. The authors work out the mechanism behind this increase in fecundity. They show that in response to EB exposure, the expression of its target receptor, GluCl, increases. This, they show, results in an increase in the expression of genes that regulate the synthesis of juvenile hormone (JH) and JH itself, which, in turn, results in enhanced egg-production and egg-laying. Interestingly, these effects of EB exposure are species-specific, as the authors report that other species of plant hoppers either don't show enhanced fecundity or show reduced fecundity. As the authors point out, it is unclear how an increase in GluCl levels could result in increased JH regulatory genes.

We greatly appreciate your valuable comments and constructive suggestion to our work. We will try to figure out how EB interacts with its molecular target GluCl and then increases JH regulatory genes in the future work using Drosophila as models.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Overall, the molecular experiments are very poorly designed and can at best be termed superficial. There are several contradictions within the paper and no discussion or explanation has been provided for that.

The authors should consider a thorough revision.

Thank you for your comments. We have thoroughly revised the paper according to your suggestions and added further experiments and explanations of our results in the discussion parts.

Reviewer #2 (Recommendations For The Authors):

It would help the reader to have more schematics along with the figures. The final figure is helpful, but knowing the JH pathway, and where it acts would help with the interpretations as one reads the manuscript and the figures. The pathways represented in 4N or 5J are helpful but could be improved upon for better presentation.

It would be nice to have some discussion on how the authors think EB exposure results in an increase in GluCl expression, and how that in turn affects the expression of so many genes.

Thank you for your comments. We have thoroughly revised the paper according to your suggestions and added further experiments and explanations of how we think EB exposure results in an increase in JH titer and other genes in the discussion parts. We have added the test on lines 753-761.

References

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Fu, B., Liang, J., Hu, J., Du, T., Tan, Q., He, C., Wei, X., Gong, P., Yang, J., Liu, S., Huang, M., Gui, L., Liu, K., Zhou, X., Nauen, R., Bass, C., Yang, X., Zhang, Y., 2024. GPCR–MAPK signaling pathways underpin fitness trade-offs in whitefly. Proceedings of the National Academy of Sciences 121, e2402407121.

Gandara, L., Jacoby, R., Laurent, F., Spatuzzi, M., Vlachopoulos, N., Borst, N.O., Ekmen, G., Potel, C.M., Garrido-Rodriguez, M., Böhmert, A.L., Misunou, N., Bartmanski, B.J., Li, X.C., Kutra, D., Hériché, J.-K., Tischer, C., Zimmermann-Kogadeeva, M., Ingham, V.A., Savitski, M.M., Masson, J.-B., Zimmermann, M., Crocker, J., 2024. Pervasive sublethal effects of agrochemicals on insects at environmentally relevant concentrations. Science 386, 446-453.

Gong, Y., Cheng, S., Desneux, N., Gao, X., Xiu, X., Wang, F., Hou, M., 2022. Transgenerational hormesis effects of nitenpyram on fitness and insecticide tolerance/resistance of Nilaparvata lugens. Journal of Pest Science.

Hu, B., Huang, H., Hu, S., Ren, M., Wei, Q., Tian, X., Esmail Abdalla Elzaki, M., Bass, C., Su, J., Reddy Palli, S., 2021. Changes in both trans- and cis-regulatory elements mediate insecticide resistance in a lepidopteron pest, Spodoptera exigua. PLOS Genetics 17, e1009403.

Jiang, H., Meng, X., Zhang, N., Ge, H., Wei, J., Qian, K., Zheng, Y., Park, Y., Reddy Palli, S., Wang, J., 2023. The pleiotropic AMPK–CncC signaling pathway regulates the trade-off between detoxification and reproduction. Proceedings of the National Academy of Sciences 120, e2214038120.

Ko, K.I., Root, C.M., Lindsay, S.A., Zaninovich, O.A., Shepherd, A.K., Wasserman, S.A., Kim, S.M., Wang, J.W., 2015. Starvation promotes concerted modulation of appetitive olfactory behavior via parallel neuromodulatory circuits. eLife 4, e08298.

Li, Z., Wang, Y., Qin, Q., Chen, L., Dang, X., Ma, Z., Zhou, Z., 2023. Imidacloprid disrupts larval molting regulation and nutrient energy metabolism, causing developmental delay in honey bee Apis mellifera. eLife

Martelli, F., Hernandes, N.H., Zuo, Z., Wang, J., Wong, C.-O., Karagas, N.E., Roessner, U., Rupasinghe, T., Robin, C., Venkatachalam, K., Perry, T., Batterham, P., Bellen, H.J., 2022. Low doses of the organic insecticide spinosad trigger lysosomal defects, elevated ROS, lipid dysregulation, and neurodegeneration in flies. eLife 11, e73812.

Peng, Y.C., Sheng, C.W., Casida, J.E., Zhao, C.Q., Han, Z.J., 2017. Ryanodine receptor genes of the rice stem borer, Chilo suppressalis: Molecular cloning, alternative splicing and expression profiling. Pestic. Biochem. Physiol. 135, 69-77.

Root, Cory M., Ko, Kang I., Jafari, A., Wang, Jing W., 2011. Presynaptic facilitation by neuropeptide signaling mediates odor-driven food search. Cell 145, 133-144.

Zhang, Y., Wang, X., Yang, B., Hu, Y., Huang, L., Bass, C., Liu, Z., 2015. Reduction in mRNA and protein expression of a nicotinic acetylcholine receptor α8 subunit is associated with resistance to imidacloprid in the brown planthopper, Nilaparvata lugens. Journal of Neurochemistry 135, 686-694.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors bring together implanted radiofrequency coils, high-field MRI imaging, awake animal imaging, and sensory stimulation methods in a technological demonstration. The results are very detailed descriptions of the sensory systems under investigation.

Strengths:

- The maps are qualitatively excellent for rodent whole-brain imaging. - The design of the holder and the coil is pretty clever.

Weaknesses:

- Some unexpected regions appear on the whole brain maps, and the discussion of these regions is succinct.

- The authors do not make the work and e ort to train the animals and average the data from several hundred trials apparent enough. This is important for any reader who would like to consider implementing this technology.

- The data is not available. This does not let the readers make their own assessment of the results.

Thank you for the comments on this manuscript. We have provided more detailed discussion of the unexpected regions(page 18 – line 491-494) and training procedures(page7-9 – line 172-236). We also uploaded the datasets to OpenNeuro 

Whisker (https://doi.org/10.18112/openneuro.ds005496.v1.0.1),  Visual (https://doi.org/10.18112/openneuro.ds005497.v1.0.0) and Zenodo:

SNR Line Profile Data & Data Processing Scripts:  (https://zenodo.org/doi/10.5281/zenodo.13821455). 

Reviewer #2 (Public Review):

Summary:

The manuscript by Hike et al. entitled 'High-resolution awake mouse fMRI at 14 Tesla' describes the implementation of awake mouse BOLD-fMRI at high field. This work is timely as the field of mouse fMRI is working toward collecting high-quality data from awake animals. Imaging awake subjects o ers opportunities to study brain function that are otherwise not possible under the more common anesthetized conditions. Not to mention the confounding e  ects that anesthesia has on neurovascular coupling. What has made progress in this area slow (relative to other imaging approaches like optical imaging) is the environment within the MRI scanner (high acoustic noise) - as well as the intolerance of head and body motion. This work adds to a relatively small, but quickly growing literature on awake mouse fMRI. The findings in the study include testing of an implanted head-coil (for MRI data reception). Two designs are described and the SNR of these units at 9.4T and 14T are reported. Further, responses to visual as well as whisker stimulation recorded in acclimated awake mice are shown. The most interesting finding, and most novel, is the observation that mice seem to learn to anticipate the presentation of the stimulus - as demonstrated by activations evident ~6 seconds prior to the presentation of the stimulus when stimuli are delivered at regular intervals (but not when stimuli are presented at random intervals). These kinds of studies are very challenging to do. The surgical preparation and length of time invested into training animals are grueling. I also see this work as a step in the right direction and evidence of the foundations for lots of interesting future work. However, I also found a few shortcomings listed below.

Weaknesses:

(1) The surface coil, although o ering a great SNR boost at the surface, ultimately comes at a cost of lower SNR in deeper more removed brain regions in comparison to commercially available Bruker coils (at room temperature). This should be quantified. A rough comparison in SNR is drawn between the implanted coils and the Bruker Cryoprobe - this should be a quantitative comparison (if possible) - including any di erences in SNR in deeper brain structures. There are drawbacks to the Cryoprobe, which can be discussed, but a more thorough comparison between the implanted coils, and other existing options should be provided (the Cryoprobe has been used previously in awake mouse experiments(Sensory evoked fMRI paradigms in awake mice - Chen, Physiological e ects of a habituation procedure for functional MRI in awake mice using a cryogenic radiofrequency probe – Yoshida, PREVIOUS REFERENCE). Further, the details of how to build the implanted coils should be provided (shared) - this should include a parts list as well as detailed instructions on how to build the units. Also, how expensive are they? And can they be reused?

Thank you for the comment. We did not use a Bruker Cryoprobe for this work but rather a Bruker 4array surface coil. We are unable to compare to a cryoprobe since we do not have access to one for our system. A comparison to previously published data using different scanners could be possible but would require the sequence contain identical parameters to avoid introducing an uncontrollable variable, we are planning to recruit different laboratories to test the implanted RF coils with their existing cryoprobes in the future study. 

We have included an updated figure comparing SNR at different depths across the Bruker 4-array coil and the implanted RF coils. As shown in Supplementary Figure 7B, there is significant SNR enhancement up to 4 mm cortical depth for both single loop and Figure 8 implanted RF coils in comparison to the Bruker 4-array coil.

Author response image 1.

Comparison between implanted and commercial coils. A shows representative coils in the single loop (left) and figure 8 styles (right). Supplementary Table 1 provides a parts list and cost for making these coils and Supplementary Figure 1 provides a circuit diagram to assemble. B presents the SNR line profile values as a function of distance from Pia Matter for each coil tested at 9.4T: commercial phased array surface coil (4 Array), implanted single loop, and implanted figure 8. SNR values were calculated by dividing the signal by the standard deviation of the noise. C-E shows a representative FLASH image with line profile of SNR measurements from each of the coils used to create the graph seen in B. Clear visual improvement in SNR can be seen in figures C-E. C – Commercial phased array. D – Single loop at 9.4T. E – Figure 8 at 9.4T. (N4 array = 6, Nsingle loop = 5, Nfigure 8 = 5)

Additionally, we have added a supplementary figure (supp fig 1) of a circuit diagram, in an effort to disseminate the prototype design of the coils to other laboratories. We have included a detailed parts list with the cost for construction of the coils configured for our scanner(supp table 1). These specifics though would need to be adjusted to the precise field strength/bore size/animal the coil was being built for. As for reusability, the copper wire is cemented to the animal skull and this implantable coil should be considered as consumables for the awake mouse experiments, though the PCB parts can be retrieved.  

(2) In the introduction, the authors state that "Awake mouse fMRI has been well investigated". I disagree with this statement and others in the manuscript that gives the reader the impression that awake experiments are not a challenging and unresolved approach to fMRI experiments in mice (or rodents). Although there are multiple labs (maybe 15 worldwide) that have conducted awake mouse experiments (with varying degrees of success/thoroughness), we are far from a standardized approach. This is a strength of the current work and should be highlighted as such. I encourage the authors to read the recent systematic review that was published on this topic in Cerebral Cortex by Mandino et al. There are several elements in there that should influence the tone of this piece including awake mouse implementations with the Bruker Cryoprobe, prevalence of surgical preparations, and evaluations of stress.

Thank you for the comment. We agree with the reviewer that the current stage of awake mouse fMRI studies remains to be improved.  And, we have revised the Introduction to highlight the state-of-theart of awake mouse fMRI (Page 4 – line 81-88). 

(3) The authors also comment on implanted coils reducing animal stress - I don't know where this comment is coming from, as this has not been reported in the literature (to my knowledge) and the authors don't appear to have evaluated stress in their mice. 

Since question 3 and 4 are highly related to the acclimation procedures, we will answer the two questions together.   

(4) Following on the above point, measures of motion, stress, and more details on the acclimation procedure that was implemented in this study should be included.

We thank the reviewer to raise the animal training issues.  

During the animal training, we have measured both pupil dynamic and eye motion features from training sessions, of which the detailed procedure is described in Methods (page 7-9 – line 172236). 

The training procedure is carried out over a total of 5 weeks with four phases of training: i. Holding animal in hands, ii. Head-fixation and pupillometry, iii. Head-fixation and pupillometry with mockMRI acoustic exposure, iv. Head-fixation and pupillometry with Echo-Planar-Imaging (EPI) in the MR scanner.

Author response table 1.

As shown in Supp Fig 2B, the spectral power of pupil dynamics (<0.02Hz) and eye movements gradually increased as a function of the training time for head-fixed mice exposed to the mock MRI acoustic environment during phase 3.  In phase 4, when head-fixed mice were put into the scanner for the first time, both eye movements and pupil dynamics were initially reduced during scanning but recovered to an acclimated state on Day 2, similar to the level on Day 8 of phase 3.  These behavioral outputs would provide an alternative way to monitor the stress levels of the mice. 

Author response image 2.

The eye movements (A) and power spectra of pupil dynamics (<0.02Hz) (B) change during different training phases.

It should be noted that stress may be related to increased frequency of eye blinking or twitching movements in human subjects(1–3). Whereas, the eyeblink of head-fixed mice has been used for behavioral conditioning to investigate motor learning in normal behaving mice(4–6). Importantly, head-fixed mouse studies have shown that eye movements are significantly reduced compared to the free-moving mice(7). The increased eye movement during acclimation process would indicate an alleviated stress level of the head-fixed mice in our cases. Meanwhile, stress-related pupillary dilation could dominate the pupil dynamics at the early phase of training(8). We have observed a gradually increased pupil dynamic power spectrum at the ultra-slow frequency during phase 3, presenting the alleviated stress-related pupil dilation but recovered pupil dynamics to other factors, including arousal, locomotion, startles, etc. in normal behaving mice.  Despite the extensive training procedure of the present work in comparison to the existing awake mouse fMRI studies (training strategies for awake mice fMRI have been reviewed by Mandino et al. to show the overall training duration of existing studies(9)), the stress remains a confounding factor for the brain functional mapping in head-fixed mice. In particular, a recent study(10) shows that the corticosterone concentration in the blood samples of head-fixed mice is significantly reduced on Day 25 following the training but remains higher than in the control mice. In the discussion section, we have discussed the potential issues of stress-related confounding factors for awake mouse fMRI studies (Page 16 – lines 436-458). 

(1) A. Marcos-Ramiro, D. Pizarro-Perez, M. Marron-Romera, D. Gatica-Perez, Automatic blinking detection towards stress discovery. ICMI 2014 - Proceedings of the 2014 International Conference on Multimodal Interaction 307–310 (2014). https://doi.org/10.1145/2663204.2663239/SUPPL_FILE/ICMI1520.MP4.

(2) M. Haak, S. Bos, S. Panic, L. Rothkrantz, DETECTING STRESS USING EYE BLINKS AND BRAIN ACTIVITY FROM EEG SIGNALS. Lance 21, 76 (2009).

(3) E. Del Carretto Di Ponti E Sessam, Exploring the impact of Stress and Cognitive Workload on Eye Movements: A Preliminary Study. (2023).

(4) S. A. Heiney, M. P. Wohl, S. N. Chettih, L. I. Ru olo, J. F. Medina, Cerebellar-dependent expression of motor learning during eyeblink conditioning in head-fixed mice. J Neurosci 34, 14845–14853 (2014).

(5) S. N. Chettih, S. D. Mcdougle, L. I. Ruffolo, J. F. Medina, Adaptive timing of motor output in the mouse: The role of movement oscillations in eyelid conditioning. Front Integr Neurosci 5, 12996 (2011).

(6) J. J. Siegel, et al., Trace Eyeblink Conditioning in Mice Is Dependent upon the Dorsal Medial Prefrontal Cortex, Cerebellum, and Amygdala: Behavioral Characterization and Functional Circuitry. eNeuro 2, 51–65 (2015).

(7) A. F. Meyer, J. O’Keefe, J. Poort, Two Distinct Types of Eye-Head Coupling in Freely Moving Mice. Current Biology 30, 2116-2130.e6 (2020).

(8) H. Zeng, Y. Jiang, S. Beer-Hammer, X. Yu, Awake Mouse fMRI and Pupillary Recordings in the UltraHigh Magnetic Field. Front Neurosci 16, 886709 (2022).

(9) F. Mandino, S. Vujic, J. Grandjean, E. M. R. Lake, Where do we stand on fMRI in awake mice? Cereb Cortex 34 (2024).

(10) K. Juczewski, J. A. Koussa, A. J. Kesner, J. O. Lee, D. M. Lovinger, Stress and behavioral correlates in the head-fixed method: stress measurements, habituation dynamics, locomotion, and motor-skill learning in mice. Scientific Reports 2020 10:1 10, 1–19 (2020).

(5) It wasn't clear to me at what times the loop versus "Figure 8" coil was being used, nor how many mice (or how much data) were included in each experiment/plot. There is also no mention of biological sex.

Thank you for the comment. We have clarified sex and number. The figure 8 coil was only used as part of development to show the improvement of the coil design for cortical measurements. The detailed information is described in Method (Page 6 – line 127-129 & Page 10 – line 269-270). Additionally animal numbers have been included in the figure captions.

(6) Building on the points above, the manuscript overall lacks experimental detail (especially since the format has the results prior to the methods).

Thank you for the comment. We have modified the manuscript to increase the experimental detail and moved the methods section before the results.

(7) An observation is made in the manuscript that there is an appreciable amount of negative BOLD signal. The authors speculate that this may come from astrocyte-mediated BOLD during brain state changes (and cite anesthetized rat and non-human primate experiments). This is very strange to me. First, the negative BOLD signal is not plotted (please do this), further, there are studies in awake mice that measure astrocyte activation eliciting positive BOLD responses (see Takata et al. in Glia, 2017).

We thank the reviewer to raise the negative BOLD fMRI observation issue.  We added a subplot of the negative BOLD signal changes in the revised Figure 4. This negative BOLD signals across cortical areas could be coupled with brain state changes upon air-pu -induced startle responses. Our future studies are focusing on elucidating the brain-wide activity changes of awake mice with fMRI.  We also provide a detailed discussion of the potential mechanism underlying the negative BOLD fMRI signals. First, as reported in the paper (suggested  by the reviewer),  astrocytic Ca2+ transients coincide with positive BOLD responses in the activated cortical areas, which is aligning with the neurovascular coupling (NVC) mechanism. However, there is emerging evidence to show that astrocytic Ca2+ transients are coupled with both positive and negative BOLD responses in anesthetized rats(11) and awake mice(12). An intriguing observation is that cortex-wide negative BOLD signals coupled with the spontaneous astrocytic Ca2+ transients could co-exist with the positive BOLD signal detected at the activated cortex.  Studies have shown that astrocytes are involved in regulating brain state changes(13), in particular, during locomotion(14) and startle responses(15). These brain state-dependent global negative BOLD responses are also related to the arousal changes of both non-human primates(16) and human subjects(17).  The established awake mouse fMRI platform with ultra-high spatial resolution will enable the brain-wide activity mapping of the functional nuclei contributing to the brain state changes of head-fixed awake mice in future studies. (Page 17-18 – Line 478-490)

(11) M. Wang, Y. He, T. J. Sejnowski, X. Yu, Brain-state dependent astrocytic Ca2+ signals are coupled to both positive and negative BOLD-fMRI signals. Proc Natl Acad Sci U S A 115, E1647–E1656 (2018).

(12) C. Tong, Y. Zou, Y. Xia, W. Li, Z. Liang, Astrocytic calcium signal bidirectionally regulated BOLD-fMRI signals in awake mice in Proc. Intl. Soc. Mag. Reson. Med. 32, (2024).

(13) K. E. Poskanzer, R. Yuste, Astrocytes regulate cortical state switching in vivo. Proc Natl Acad Sci U S A 113, E2675–E2684 (2016).

(14) M. Paukert, et al., Norepinephrine controls astroglial responsiveness to local circuit activity. Neuron 82, 1263–1270 (2014).

(15) R. Srinivasan, et al., Ca2+ signaling in astrocytes from IP3R2−/− mice in brain slices and during startle responses in vivo. Nat Neurosci 18, 708 (2015).

(16) C. Chang, et al., Tracking brain arousal fluctuations with fMRI. Proc Natl Acad Sci U S A 113, 4518– 4523 (2016).

(17) B. Setzer, et al., A temporal sequence of thalamic activity unfolds at transitions in behavioral arousal state. Nat Commun 13 (2022).

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I really enjoyed this work. The maps shown are among the best-quality maps out there. Here are suggestions to the authors.

(1) Both the ACA and VRA are rather unexpected. The authors explain these briefly as being part of the associative cortical areas. Both the ACA and VRA are not canonical associative areas (or at least not to us). This warrants a stronger discussion.

To verify both ACA and VRA as associate areas, we provide the  connectivity map projections from the Allen Brain Atlas (seen below). These projections are derived from a Cre-dependent AAV tracing of axonal projections. We have included an explanation of this in the introduction. 

Author response image 3.

Representative images are shown indicating connections between the barrel cortex and retrosplenial area from an injection in the barrel cortex (Left panel) as well as the visual cortex and cingulate connection from an injection in the visual cortex (Right panel). Images are of connectivity map projections from the Allen Brain Atlas derived from a Cre-dependent AAV tracing of axonal projections

(2) This is a lot of work. But looking at the figures, this is not obvious. We read in the caption that several hundred trials were used. It would be good to also specify how many mice. It would be clearer to represent this info in the figure as well to support the fact that this is not a trivial acquisition.

Thank the reviewer to raise the e ort issue. We have edited the figure to include this information and included the numbers in the text as well

(3) The training protocol is seemingly extensive, but this is only visible by following another reference. Including a description in this work would help the reader make sense of the effort that went into this work.

We thank the reviewer to raise the training protocol issue. We have more thoroughly discussed the training method used for this study (page 7-9 – line 172-236)

(4) I really would love to see that dataset made freely available - this should be the norm.

The datasets have been uploaded to OpenNeuro 

Whisker (https://doi.org/10.18112/openneuro.ds005496.v1.0.1),  Visual (https://doi.org/10.18112/openneuro.ds005497.v1.0.0) and Zenodo:

SNR Line Profile Data & Data Processing Scripts: 

(https://zenodo.org/doi/10.5281/zenodo.13821455). 

(page 21 – line 573-579)

Reviewer #2 (Recommendations For The Authors):

(1) I'm a little confused about the stimulation paradigm and the effect of it causing an effective 2second TR (which is on the long side) - please elaborate (a figure might be helpful). The paradigm for visual stimulation also seems elaborate, can you please explain the logic and how it was developed?

Thank you for raising the detailed stimulation paradigm issues. The stimulation paradigm is independent and does not interfere with the setup of the effective 2-second TR. The 2-second TR is based on the usage of 2-segment EPI, each with a TR of 1-second. The application of 2-segment paradigm enables the echo spacing with 0.52 ms with effective image bandwidth with 3858Hz, assuring less image distortion.  The stimulation paradigm was defined by an “8s on, 32s o ” epoch such to elicit a strong BOLD response and could be used for any reasonable TR duration. 

We have included a figure outlining the stimulation paradigm (Supp Fig. 3)

(2) I had difficulties viewing the movies (on my MAC).

Thank you for this note. We have re-upload the videos in .mov format

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this study, the authors engineer the endogenous left boundary of the Drosophila eve TAD, replacing the endogenous Nhomie boundary by either a neutral DNA, a wildtype Nhomie boundary, an inverted Nhomie boundary, or a second copy of the Homie boundary. They perform Micro-C on young embryos and conclude that endogenous Nhomie and Homie boundaries flanking eve pair with head-to-tail directionality to form a chromosomal stem loop. Abrogating the Nhomie boundary leads to ectopic activation of genes in the former neighboring TAD by eve embryonic stripe enhancers. Replacing Nhomie by an inverted version or by Homie (which pairs with itself head-to-head) transformed the stem loop into a circle loop. An important finding was that stem and circle loops differentially impact endogenous gene regulation both within the eve TAD and in the TADs bracketing eve. Intriguingly, an eve TAD with a circle loop configuration leads to ectopic activation of flanking genes by eve enhancers - indicating compromised regulatory boundary activity despite the presence of an eve TAD with intact left and right boundaries.

Strengths:

Overall, the results obtained are of high-quality and are meticulously discussed. This work advances our fundamental understanding of how 3D genome topologies affect enhancer-promoter communication.

Weaknesses:

Though convincingly demonstrated at eve, the generalizability of TAD formation by directional boundary pairing remains unclear, though the authors propose this mechanism could underly the formation of all TADs in Drosophila and possibly even in mammals. Strong and ample evidence has been obtained to date that cohesin-mediated chromosomal loop extrusion explains the formation of a large fraction of TADs in mammals. 

(1.1) The difficultly with most all of the studies on mammal TADs, cohesin and CTCF roadblocks is that the sequencing depth is not sufficient, and large bin sizes (>1 kb) are needed to visualize chromosome architecture.  The resulting contact profiles show TAD neighborhoods, not actual TADs.

The problem with these studies is illustrated by comparing the contact profiles of mammalian MicroC data sets at different bin sizes in Author response image 1.  In this figure, the darkness of the “pixels” in panels E, F, G and H was enhanced by reducing brightness in photoshop.

Author response image 1.

Mammalian MicroC profiles different bun sizes

Panels A and C show “TADs” using bin sizes typical of most mammalian studies (see Krietenstein et al. (2023) (Krietenstein et al. 2020)).  At this level of resolution, TADs, the “trees” that are the building blocks of chromosomes, are not visible.  Instead, what is seen are TAD neighborhoods or “forests”.  Each neighborhood consists of several dozen individual TADs.  The large bins in these panels also artificially accentuated TAD:TAD interactions, generating a series of “stripes” and “dots” that correspond to TADs bumping into each other and sequences getting crosslinked.  For example, in panel A there is prominent stripe on the edge of a “TAD” (blue arrow).  In panel C, this stripe resolves into a series of dots arranged as parallel, but interrupted “stripes” (green and blue arrows).  At the next level of resolution, it can be seen that the stripe marked by the blue arrow and magenta asterisk is generated by contacts between the left boundary of the TAD indicated by the magenta bar with sequences in a TAD (blue bar) ~180 kb way.  While dots and stripes are prominent features in contact profiles visualized with larger bin sizes (A and C), the actual TADs that are observed with a bin size of 200 bp (examples are underlined by black bars in panel G) are not bordered by stripes, nor are they topped by obvious dots.  The one possible exception is the dot that appears at the top of the volcano triangle underlined with magenta.

The chromosome 1 DNA segment from the MicroC data of Hseih et al. (2023) (Hsieh et al. 2020) shows a putative volcano triangle with a plume (indicated by a V in Author response image 1 panels D, F and H).  Sequences in the V TAD don’t crosslink with their immediate neighbors, and this gives a “plume” above the volcano triangle, as indicate by the light blue asterisk in panels D, F and H.  Interestingly the V TAD does contact two distant TADs, U on the left and W on the right. The U TAD is ~550 kb from V, and the region of contact is indicated by the black arrow.  The W TAD is ~585 kb from V, and the region of contact is indicated by the magenta arrow.  While the plume still seems to be visible with a bin size of 400 bp (light blue asterisk), it is hard to discern when the bin size is 200 bp, as there are not enough reads.

The evidence demonstrating that cohesin is required for TAD formation/maintenance is based on low resolution Hi-C data, and the effects that are observed are on TAD neighborhoods (forests) and not TADs (trees).  In fact, there is published evidence that cohesin is not required in mammals for TAD formation/maintenance.  In an experiment from Goel et al. 2023 the authors depleted the cohesin component Rad21 and then visualized the effects on TAD organization using the high resolution region capture MicroC (RCMC) protocol.  The MicroC contact map in this figure visualizes a ~250 kb DNA segment around the Ppm1pg locus at 250 bp resolution.  On the right side of the diagonal is the untreated control, while the left side shows the MicroC profile of the same region after Rad21 depletion.  The authors indicated that there was a 97% depletion of Rad21 in their experiment.  However, as is evident from a comparison of the experimental and control, loss of Rad21 has no apparent effect on the TAD organization of this mammalian DNA segment.

Several other features are worth noting.  First, unlike the MicroC experiments shown in Author response image 1, there are dots at the apex of the TADs in this chromosomal segment.  In the MicroC protocol, fixed chromatin is digested to mononucleosomes by extensive MNase digestion.  The resulting DNA fragments are then ligated, and dinucleosome-length fragments are isolated and sequenced. 

DNA sequences that are nucleosome free in chromatin (which would be promoters, enhancers, silencers and boundary elements) are typically digested to oligonucleotides in this procedure and won’t be recovered. This means that the dots shown here must correspond to mononucleosome-length elements that are MNase resistant.  This is also true for the dots in the MicroC contact profiles of the Drosophila Abd-B regulatory domain (see Fig. 2B in the paper).  Second, the TADs are connected to each other by 45o stripes (see blue and green arrowheads).  While it is not clear from this experiment whether the stipes are generated by an active mechanism (enzyme) or by some “passive” mechanism (e.g., sliding), the stripes in this chromosomal segment are not generated by cohesin, as they are unperturbed by Rad21 depletion.  Third, there are no volcano triangles with plumes in this chromosomal DNA segment.  Instead, the contact patterns (purple and green asterisks) between neighboring TADs closely resemble those seen for the Abd-B regulatory domains (compare Goel et al. 2023 with Fig. 2B in the paper).  This similarity suggests that the TADs in and around Ppm1g may be circle-loops, not stem-loops.  As volcano triangles with plumes also seem to be rare in the MicroC data sets of Krietenstein et al. (Krietenstein et al. 2020) and Hesih et al. (Hsieh et al. 2020) (with the caveat that these data sets are low resolution: see Author response image 1), it is possible that much of the mammalian genome is assembled into circle-loop TADs, a topology that can’t be generated by the cohesin loop extrusion (bolo tie clip) /CTCF roadblock model.

While Rad21 depletion has no apparent effect on TADs, it does appear to impact TAD neighborhoods.  This is in a supplemental figure in Goel et al. (Goel et al. 2023).  In this figure, TADs in the Ppm1g region of chromosome 5 are visualized with bin sizes of 5 kb and 1 kb.  A 1.2 Mb DNA segment is shown for the 5 kb bin size, while an 800 kb DNA segment is shown for the 1 kb bin size.  As can be seen from comparing the MicroC profiles in Author response image 2 with that in Goel et al. 2023, individual TADs are not visible.  Instead, the individual TADs are binned into large TAD “neighborhoods” that consist of several dozen or more TADs.

Unlike the individual TADs shown in Goel et al. 2023, the TAD neighborhoods in Author response image 2 are sensitive to Rad21 depletion.  The effects of Rad21 depletion can be seen by comparing the relative pixel density inside the blue lines before (above the diagonal) and after (below the diagonal) auxin-induced Rad21 degradation.  The reduction in pixel density is greatest for more distant TAD:TAD contacts (farthest from the diagonal).  By contrast, the TADs themselves are unaffected (Goel et al. 2023), as are contacts between individual TADs and their immediate neighbors.  In addition, contacts between partially overlapping TAD neighborhoods are also lost.  At this point it isn’t clear why contacts between distant TADs in the same neighborhood are lost when Rad21 is depleted; however, a plausible speculation is that it is related to the functioning of cohesin in holding newly replicated DNAs together until mitosis and whatever other role it might have in chromosome condensation.

Author response image 2.

Ppm1g full locus chr5

Moreover, given the unique specificity with which Nhomie and Homie are known to pair (and exhibit "homing" activity), it is conceivable that formation of the eve TAD by boundary pairing represents a phenomenon observed at exceptional loci rather than a universal rule of TAD formation. Indeed, characteristic Micro-C features of the eve TAD are only observed at a restricted number of loci in the fly genome…..

(1.2) The available evidence does not support the claim that nhomie and homie are “exceptional.”  To begin with, nhomie and homie rely on precisely the same set of factors that have been implicated in the functioning of other boundaries in the fly genome.  For example, homie requires (among other factors) the generic boundary protein Su(Hw) for insulation and long-distance interactions (Fujioka et al. 2024).  (This is also true of nhomie: unpublished data.)  The Su(Hw) protein (like other fly polydactyl zinc finger proteins) can engage in distant interactions.  This was first shown by Sigrist and Pirrotta (Sigrist and Pirrotta 1997), who found that the su(Hw) element from the gypsy transposon can mediate long-distance regulatory interactions (PRE dependent silencing) between transgenes inserted at different sites on homologous chromosomes (trans interactions) and at sites on different chromosomes.

The ability to mediate long-distance interactions is not unique to the su(Hw) element, or homie and nhomie.  Muller et al. (Muller et al. 1999) found that the Mcp boundary from the Drosophila BX-C is also able to engage in long-distance regulatory interactions—both PRE-dependent silencing of mini-white and enhancer activation of mini-white and yellow.  The functioning of the Mcp boundary depends upon two other generic insulator proteins, Pita and the fly CTCF homolog (Kyrchanova et al. 2017).  Like Su(Hw) both are polydactyl zinc finger proteins, and they resemble the mammalian CTCF protein in that their N-terminal domain mediates multimerization (Bonchuk et al. 2020; Zolotarev et al. 2016).  Figure 6 from Muller et el. 1999 shows PRE-dependent “pairing sensitive silencing” interactions between transgenes carrying a mini-white reporter, the Mcp and scs’ (Beaf dependent)(Hart et al. 1997) boundary elements, and a PRE closely linked to Mcp.  In this experiment flies homozygous for different transgene inserts were mated and the eye color was examined in their transheterozygous progeny.  As indicated in the figure, the strongest trans-silencing interactions were observed for inserts on the same chromosomal arm; however, transgenes inserted on the left arm of chromosome 3 can interact across the centromere with transgenes inserted on the right arm of chromosome 3. 

Figure 5C (left) from Muller et el. 1999 shows a trans-silencing interaction between w#11.102 at 84D and w#11.16 approximately 5.8 Mb away, at 87D.  Figure 5C (right) shows a trans-silencing interaction across the centromere between w#14.29 on the left arm of chromosome 3 at 78F and w#11.102 on the right arm of chromosome 3 at 84D. The eye color phenotype of mini-white-containing transgenes is usually additive: homozygyous inserts have twice as dark eye color as the corresponding hemizygous inserts.  Likewise, in flies trans-_heterozygous for _mini-white transgenes inserted at different sites, the eye color is equivalent to the sum of the two transgenes.  This is not true when mini-white transgenes are silenced by PREs.  In the combination shown in panel A, the t_rans-_heterozygous fly has a lighter eye color than either of the parents.  In the combination in panel B, the _trans-_heterozygous fly is slightly lighter than either parent.

As evident from the diagram in Figure 6 from Muller et el. 1999, all of the transgenes inserted on the 3rd chromosome that were tested were able to participate in long distance (>Mbs) regulatory interactions.  On the other hand, not all possible pairwise interactions are observed.  This would suggest that potential interactions depend upon the large scale (Mb) 3D folding of the 3rd chromosome.

When the scs boundary (Zw5 dependent) (Gaszner et al. 1999) was added to the transgene to give sMws’, it further enhanced the ability of distant transgenes to find each other and pair.  All eight of the sMws’ inserts that were tested were able to interact with at least one other sMws’ insert on a different chromosome and silence mini-white.  Vazquez et al. () subsequently tagged the sMws’ transgene with LacO sequences (ps0Mws’) and visualized pairing interactions in imaginal discs.  Trans-heterozygous combinations on the same chromosome were found paired in 94-99% of the disc nuclei, while a trans-heterozygous combination on different chromosomes was found paired in 96% of the nuclei (Table 3 from Vazquez et al. 2006).  Vazquez et al. also examined a combination of four transgenes inserted on the same chromosome (two at the same insertion site, and two at different insertion sites).  In this case, all four transgenes were clustered together in 94% of the nuclei (Table 3 from Vazquez et al. 2006).  Their studies also suggest that the distant transgenes remain paired for at least several hours.  A similar experiment was done by Li et al. (Li et al. 2011), except that the transgene contained only a single boundary, Mcp or Fab-7.  While pairing was still observed in trans-heterozygotes, the frequency was reduced without scs and scs’.

It is worth pointing out that there is no plausible mechanism in which cohesin could extrude a loop through hundreds of intervening TADs, across the centromere (ff#13.101_ßà_w#11.102: Figure 6 from Muller et el. 1999; w#14.29_ßà_w#11.02: Figure 6 from Muller et el. 1999 and 5) and come to a halt when it “encounters” Mcp containing transgenes on different homologs.  The same is true for Mcp-dependent pairing interactions in cis (Fig. 7 in Muller et al. (Muller et al. 1999)) or Mcp-dependent pairing interactions between transgenes inserted on different chromosomes (Fig. 8 in Muller et al. (Muller et al. 1999); Line 8 in Table 3 from Vazquez et al. 2006). 

These are not the only boundaries that can engage in long-distance pairing.  Mohana et al. (Mohana et al. 2023) identified nearly 60 meta-loops, many of which appear to be formed by the pairing of TAD boundary elements.  Two examples (at 200 bp resolution from 12-16 hr embryos) are shown in Author response image 3.

Author response image 3.

Metaloops on the 2nd and 3rd chromosomes: circle-loops and multiple stem-loops

One of these meta-loops (panel A) is generated by the pairing of two TAD boundaries on the 2nd chromosome.  The first boundary, blue, (indicated by blue arrow) is located at ~2,006, 500 bp between a small TAD containing the Nplp4 and CG15353 genes and a larger TAD containing 3 genes, CG33543, Obp22a and Npc2a.  Nplp4 encodes a neuropeptide.  The functions of CG15354 and CG33543 are unknown.  Obp22a encodes an odorant binding protein, while Npc2a encodes the Niemann-Pick type C-2a protein which is involved sterol homeostasis.  The other boundary (purple: indicated by purple arrow) is located between two TADs 2.8 Mb away at 4,794,250 bp.  The upstream TAD contains the fipi gene (CG15630) which has neuronal functions in male courtship, while the downstream TAD contains CG3294, which is thought to be a spliceosome component, and schlaff (slf) which encodes a chitin binding protein.  As illustrated in the accompanying diagram, the blue boundary pairs with the purple boundary in a head-to-head orientation, generating a ~2.8 Mb loop with a circle-loop topology.  As a result of this pairing, the multi-gene (CG33543, Obp22a and Npc2a) TAD upstream of the blue boundary interacts with the CG15630 TAD upstream of the purple boundary.  Conversely the small Nplp4:CG15353 TAD downstream of the blue boundary interacts with the CG3294:slf TAD downstream of the purple boundary.  Even if one imagined that the cohesin bolo tie clip was somehow able to extrude 2.8 Mb of chromatin and then know to stop when it encountered the blue and purple boundaries, it would’ve generated a stemloop, not a circle-loop.

The second meta-loop (panel B) is more complicated as it is generated by pairing interactions between four boundary elements.  The blue boundary (blue arrow) located ~4,801,800 bp (3L) separates a large TAD containing the RhoGEF64C gene from a small TAD containing CG7509, which encodes a predicted subunit of an extracellular carboxypeptidase.  As can be seen in the MicroC contact profile and the accompanying diagram, the blue boundary pairs with the purple boundary (purple arrow) which is located at ~7,013, 500 (3L) just upstream of the 2nd internal promoter (indicated by black arrowhead) of the Mp (Multiplexin) gene.  This pairing interaction is head-to-tail and generates a large stem-loop that spans ~2.2 Mb.  The stem-loop brings sequences upstream of the blue boundary and downstream of the purple boundary into contact (the strings below a bolo tie clip), just as was observed in the boundary bypass experiments of Muravyova et al. (Muravyova et al. 2001) and Kyrchanova et al. (Kyrchanova et al. 2008).  The physical interactions result in a box of contacts (right top) between sequences in the large RhoGEF64C TAD and sequences in a large TAD that contains an internal Mp promoter.  The second pairing interaction is between the brown boundary (brown arrow) and the green boundary (green arrow).  The brown boundary is located at ~4 805,600 bp (3L) and separates the TAD containing CG7590 from a large TAD containing CG1808 (predicted to encode an oxidoreductase) and the Dhc64C (Dynein heavy chain 64C) gene.  The green boundary is located at ~6,995,500 bp (3L), and it separates a TAD containing CG32388 and the biniou (bin) transcription factor from a TAD that contains the most distal promoter of the Mp (Multiplexin) gene (blue arrowhead).  As indicated in the diagram, the brown and green boundaries pair with each other head-to-tail, and this generates a small internal loop (and the final configuration would resemble a bolo tie with two tie clips).  This small internal loop brings the CG7590 TAD into contact with the TAD that extends from the distal Mp promoter to the 2nd internal Mp promoter.  The resulting contact profile is a rectangular box with diagonal endpoints corresponding to the paired blue:purple and brown:green boundaries.  The pairing of the brown:green boundaries also brings the TADs immediately downstream of the brown boundary and upstream of the green boundary into contact with each other, and this gives a rectangular box of interactions between the Dhc64C TAD, and sequences in the bin/CG3238 TAD.  This box is located on the lower left side of the contact map.

Since the bin and Mp meta-loops in Author response image 3B are stem-loops, they could have been generated by “sequential” cohesin loop extrusion events.  Besides the fact that cohesin extrusion of 2 Mb of chromatin and breaking through multiple intervening TAD boundaries challenges the imagination, there is no mechanism in the cohesion loop extrusion/CTCF roadblock model to explain why cohesion complex 1 would come to a halt at the purple boundary on one side and the blue boundary on the other, while cohesin complex 2 would instead stop when it hits the brown and green boundaries.  This highlights another problem with the cohesin loop extrusion/CTCF roadblock model, namely that the roadblocks are functionally autonomous: they have an intrinsic ability to block cohesin that is entirely independent of the intrinsic ability of other roadblocks in the neighborhood.  As a result, there is no mechanism for generating specificity in loop formation.  By contrast, boundary pairing interactions are by definition non-autonomous and depend on the ability of individual boundaries to pair with other boundaries: specificity is built into the model. The mechanism for pairing, and accordingly the basis for partner preferences/specificity, are reasonably well understood.  Probably the most common mechanism in flies is based on shared binding sites for architectural proteins that can form dimers or multimers (Bonchuk et al. 2021; Fedotova et al. 2017).  Flies have a large family of polydactyl zinc finger DNA binding proteins, and as noted above, many of these form dimers or multimers and also function as TAD boundary proteins.  This pairing principle was first discovered by Kyrchanova et al. (Kyrchanova et al. 2008).  This paper also showed that orientation-dependent pairing interactions is a common feature of endogenous fly boundaries.  Another mechanism for pairing is specific protein:protein interactions between different DNA binding factors (Blanton et al. 2003).  Yet a third mechanism would be proteins that bridge different DNA binding proteins together.  The boundaries that use these different mechanisms (BX-C boundaries, scs, scs’) depend upon the same sorts of proteins that are used by homie and nhomie.  Likewise, these same set of factors reappear in one combination or another in most other TAD boundaries.  As for the orientation of pairing interactions, this is most likely determined by the order of binding sites for chromosome architectural proteins in the partner boundaries.

…and many TADs lack focal 3D interactions between their boundaries.

(1.3) The idea that flies differ from mammals in that they “lack” focal 3D interactions is simply mistaken.  One of the problems with drawing this distinction is that most all of the “focal 3D interactions” seen mammalian Hi-C experiments are a consequence of binning large DNA segments in low resolution restriction enzyme-dependent experiments.  This is even true in the two “high” resolution MicroC experiments that have been published (Hsieh et al. 2020; Krietenstein et al. 2020).  As illustrated above in Author response image 1, most of the “focal 3D interactions” (the dots at the apex of TAD triangles) seen with large bin sizes (1 kb and greater) disappear when the bin size is 200 bp and TADs rather than TAD neighborhoods are being visualized.

As described in point #1.1, in the MicroC protocol, fixed chromatin is first digested to mononucloesomes by extensive MNase digestion, processed/biotinylated, and ligated to give dinucleosome-length fragments, which are then sequenced.  Regions of chromatin that are nucleosome free (promoters, enhancers, silencers, boundary elements) will typically be reduced to oligonucleotides in this procedure and will not be recovered when dinucleosome-length fragments are sequenced.  The loss of sequences from typical paired boundary elements is illustrated by the lar meta-loop shown in Author response image 4 (at 200 bp resolution).  Panels A and B show the contact profiles generated when the blue boundary (which separates two TADs that span  the Lar (Leukocyteantigen-related-like) transcription unit interacts with the purple boundary (which separates two TADs in a gene poor region ~620 kb away).  The blue and purple boundaries pair with each other head-to-head, and this pairing orientation generates yet another circle-loop.  In the circle-loop topology, sequences in the TADs upstream of both boundaries come into contact with each other, and this gives the small dark rectangular box to the upper left of the paired boundaries (Author response image 4A).  (Note that this small box corresponds to the two small TADs upstream of the blue and purple boundaries, respectively. See panel B.)  Sequences in the TADs downstream of the two boundaries also come into contact with each other, and this gives the large box to the lower right of the paired boundaries.  While this meta-loop is clearly generated by pairing interactions between the blue and purple boundaries, the interacting sequences are degraded in the MicroC protocol, and sequences corresponding to the blue and purple boundaries aren’t recovered.  This can be seen in panel B (red arrow and red arrowheads).  When a different Hi-C procedure is used (dHS-C) that captures nucleosome-free regions of chromatin that are physically linked to each other (Author response image 4C & D), the sequences in the interacting blue and purple boundaries are recovered and generate a prominent “dot” at their physical intersection (blue arrow in panel D).

Author response image 4.

Lar metaloop. Panels A & bB: MicroC. Panels C & D: dHS-C

While sequences corresponding to the blue and purple boundaries are lost in the MicroC procedure, there is at least one class of elements that engage in physical pairing interactions whose sequences are (comparatively) resistant to MNase digestion.  This class of elements includes many PREs ((Kyrchanova et al. 2018); unpublished data), the boundary bypass elements in the Abd-B region of BX-C (Kyrchanova et al. 2023; Kyrchanova et al. 2019a; Kyrchanova et al. 2019b; Postika et al. 2018), and “tethering” elements (Batut et al. 2022; Li et al. 2023).  In all of the cases tested, these elements are bound in nuclear extracts by a large (>1000 kD) GAGA factor-containing multiprotein complex called LBC.  LBC also binds to the hsp70 and eve promoters (unpublished data).  Indirect end-labeling experiments (Galloni et al. 1993; Samal et al. 1981; Udvardy and Schedl 1984) indicate that the LBC protects a ~120-180 bp DNA segment from MNase digestion.  It is likely that this is the reason why LBC-bound sequences can be recovered in MicroC experiments as dots when they are physically linked to each other.  One such example (based on the ChIP signatures of the paired elements) is indicated by the green arrow in panel B and D of Author response image 4.  Note that there are no dots corresponding to these two LBC elements within either of the TADs immediately downstream of the blue and purple boundaries.  Instead the sequences corresponding to the two LBC elements are only recovered when the two elements pair with each other over a distance of ~620 kb.  The fact that these two elements pair with each other is consistent with other findings which indicate that, like classical boundaries, LBC elements exhibit partner preferences.  In fact, LBC elements can sometimes function as TAD boundaries.  For example, the Fab-7 boundary has two LBC elements, and full Fab-7 boundary function can be reconstituted with just these two elements (Kyrchanova et al. 2018).

Reviewer #2 (Public Review):

"Chromatin Structure II: Stem-loops and circle-loops" by Ke*, Fujioka*, Schedl, and Jaynes reports a set of experiments and subsequent analyses focusing on the role of Drosophila boundary elements in shaping 3D genome structure and regulating gene expression. The authors primarily focus on the region of the fly genome containing the even skipped (eve) gene; eve is expressed in a canonical spatial pattern in fly embryos and its locus is flanked by the well-characterized neighbor of homie (nhomie) and homie boundary elements. The main focus of investigation is the orientation dependence of these boundary elements, which had been observed previously using reporter assays. In this study, the authors use Crispr/Cas9 editing followed by recombination-mediated cassette exchange to create a series of recombinant fly lines in which the nhomie boundary element is either replaced with exongenous sequence from phage 𝝀, an inversion of nhomie, or a copy of homie that has the same orientation as the endogenous homie sequence. The nhomie sequence is also regenerated in its native orientation to control for effects introduced by the transgenesis process.

The authors then perform high-resolution Micro-C to analyze 3D structure and couple this with fluorescent and colorimetric RNA in situ hybridization experiments to measure the expression of eve and nearby genes during different stages of fly development. The major findings of these experiments are that total loss of boundary sequence (replacement with 𝝀 DNA) results in major 3D structure changes and the most prominent observed gene changes, while inversion of the nhomie boundary or replacement with homie resulted in more modest effects in terms of 3D structure and gene expression changes and a distinct pattern of gene expression change from the 𝝀 DNA replacement. As the samples in which the nhomie boundary is inverted or replaced with homie have similar Micro-C profiles at the eve locus and show similar patterns of a spurious gene activation relative to the control, the observed effects appear to be driven by the relative orientation of the nhomie and homie boundary elements to one another.

Collectively, the findings reported in the manuscript are of broad interest to the 3D genome field. Although extensive work has gone into characterizing the patterns of 3D genome organization in a whole host of species, the underlying mechanisms that structure genomes and their functional consequences are still poorly understood. The perhaps best understood system, mechanistically, is the coordinated action of CTCF with the cohesin complex, which in vertebrates appears to shape 3D contact maps through a loop extrusion-pausing mechanism that relies on orientation-dependent sequence elements found at the boundaries of interacting chromatin loops.

(2.1) The notion that mammalian genome is shaped in 3D by the coordinate action of cohesin and CTCF has achieved the status of dogma in the field of chromosome structure in vertebrates.  However, as we have pointed out in #1.1, the evidence supporting this dogma is far from convincing.  To begin with, it is based on low resolution Hi-C experiments that rely on large bin sizes to visualize so-called “TADs.”  In fact, the notion that cohesin/CTCF are responsible on their own for shaping the mammalian 3D genome appears to be a result of mistaking a series of forests for the actual trees that populate each of the forests.

As illustrated in Author response image 1 above, the “TADs” that are visualized in these low resolution data sets are not TADs at all, but rather TAD neighborhoods consisting of several dozen or more individual TADs.  Moreover, the “interesting” features that are evident at low resolution (>1 kb)—the dots and stripes—largely disappear at resolutions appropriate for visualizing individual TADs (~200 bp).

In Goel et al. 2023, we presented data from one of the key experiments in Goel et al. (Goel et al. 2023).  In this experiment,  the authors used RCMC to generate high resolution (~250 bp) MicroC contact maps before and after Rad21 depletion.  Contrary to dogma, Rad21 depletion has absolutely no effect on TADs in a ~250 kb DNA segment—and these TADs look very much like the TADs we observe in the Drosophila genome, in particular in the Abd-B region of BX-C that is thought to be assembled into a series of circle-loops (see Fig. 2B).

While Goel et al. (Goel et al. 2023) observed no effect of Rad21 depletion on TADs, they found that loss of Rad21 disturbs long-distance (but not short-distance) contacts in large TAD neighborhoods when their RCMC data set is visualized using bin sizes of 5 kb and I kb.  This is shown in Author response image 2.  The significance of this finding is, however, uncertain.  It could mean that the 3D organization of large TAD neighborhoods have a special requirement for cohesin activity.  On the other hand, since cohesin functions to hold sister chromosomes together after replication until they separate during mitosis (and might also participate in mitotic condensation), it is also possible that the loss of long-range contacts in large TAD neighborhoods when Rad21 is depleted is simply a reflection of this particular activity.  Further studies will be required to address these possibilities.

As for CTCF: a careful inspection of the ChIP data in Goel et al. 2023 indicates that CTCF is not found at each and every TAD boundary.  In fact, the notion that CTCF is the be-all and end-all of TAD boundaries in mammals is truly hard to fathom.  For one, the demands for specificity in TAD formation (and in regulatory interactions) are likely much greater than those in flies, and specificity can’t be generated by a single DNA binding protein.  For another, several dozen chromosomal architectural proteins have already been identified in flies.  This means that (unlike what is thought to be true in mammals) it is possible to use a combinatorial mechanism to generate specificity in, for example, the long distance interactions in RFig 6 and 7.  As noted in #2.1 above, many of the known chromosomal architectural proteins in flies are polydactyl zinc finger proteins (just like CTCF).  There are some 200 different polydactyl zinc finger proteins in flies, and the function of only a hand full of these is known at present.  However, it seems likely that a reasonable fraction of this class of DNA binding proteins will ultimately turn out to have an architectural function of some type (Bonchuk et al. 2021; Fedotova et al. 2017).  The number of different polydactyl zinc finger protein genes in mammals is nearly 3 times that of flies.  It is really possible that of these, only CTCF is involved in shaping the 3D structure of the mammalian genome?

Despite having a CTCF paralog and cohesin, the Drosophila genome does not appear to be structure by loop extrusion-pausing. The identification of orientation-dependent elements with pronounced structural effects on genome folding thus may shed light on alternative mechanisms used to regulated genome structure, which in turn may yield insights into the significance of particular folding patterns.

(2.2) Here we would like to draw the reviewer’s and reader’s attention to Author response image 3, which shows that orientation-dependent pairing interactions have a significant impact on physical interactions between different sequences.  We would also refer the reader to two other publications.  One of these is Kyrchanova et al. (Kyrchanova et al. 2008), which was the first to demonstrate that orientation of pairing interactions matters.  The second is Fujioka et al. (Fujioka et al. 2016), which describes experiments indicating that nhomie and homie pair with each other head-to-tail and with themselves head-to-head.

On the whole, this study is comprehensive and represents a useful contribution to the 3D genome field. The transgenic lines and Micro-C datasets generated in the course of the work will be valuable resources for the research community. Moreover, the manuscript, while dense in places, is generally clearly written and comprehensive in its description of the work. However, I have a number of comments and critiques of the manuscript, mainly centering on the framing of the experiments and presentation of the Micro-C results and on manner in which the data are analyzed and reported. They are as follows:

Major Points:

(1) The authors motivate much of the introduction and results with hypothetical "stem loop" and "circle loop" models of chromosome confirmation, which they argue are reflected in the Micro-C data and help to explain the observed ISH patterns. While such structures may possibly form, the support for these specific models vs. the many alternatives is not in any way justified. For instance, no consideration is given to important biophysical properties such as persistence length, packing/scaling, and conformational entropy. As the biophysical properties of chromatin are a very trafficked topic both in terms of experimentation and computational modeling and generally considered in the analysis of chromosome conformation data, the study would be strengthened by acknowledgement of this body of work and more direct integration of its findings.

(2.3) The reviewer is not correct in claiming that “stem-loops” and “circle-loops” are “hypothetical.”  There is ample evidence that both types of loops are present in eukaryotic genomes, and that loop conformation has significant readouts in terms of not only the physical properties of TADs but also their functional properties.  Here we would draw the reviewer’s attention to Author response image 3 and Author response image 4 for examples of loops formed by the orientation-dependent pairing of yet other TAD boundary elements.  As evident from the MicroC data in these figures, circle-loops and stem-loops have readily distinguishable contact patterns.  The experiments in Fujioka et al. (Fujioka et al. 2016) demonstrate that homie and nhomie pair with each other head-to-tail, while they pair with themselves head-to-head.  The accompany paper (Bing et al. 2024) also provides evidence that loop topology is reflected both in the pattern of activation of reporters and in the MicroC contact profiles.  We would also mention again Kyrchanova et al. (Kyrchanova et al. 2008), who were the first to report orientation-dependent pairing of endogenous fly boundaries.

At this juncture it would premature to try to incorporate computational modeling of chromosome conformation in our studies.  The reason is that the experimental foundations that would be essential for building accurate models are lacking.  As should be evident from RFigs. 1-3 above, studies on mammalian chromosomes are simply not of high enough resolution to draw firm conclusions about chromosome conformation: in most studies only the forests are visible.  While the situation is better in flies, there are still too many unknown.  As just one example, it would be important to know the orientation of the boundary pairing interactions that generate each TAD.  While it is possible to infer loop topology from how TADs interact with their neighbors (a plume versus clouds), a conclusive identification of stem- and circle-loops will require a method to unambiguously determine whether a TAD boundary pairs with its neighbor head-to-head or headto-tail.

(2) Similar to Point 1, while there is a fair amount of discussion of how the observed results are or are not consistent with loop extrusion, there is no discussion of the biophysical forces that are thought to underly compartmentalization such as block-polymer co-segregation and their potential influence. I found this absence surprising, as it is generally accepted that A/B compartmentalization essentially can explain the contact maps observed in Drosophila and other non-vertebrate eukaryotes (Rowley, ..., Corces 2017; PMID 28826674). The manuscript would be strengthened by consideration of this phenomenon.

(2.4) Compartments in mammals have typically been identified and characterized using lowresolution data sets, and these studies have relied on visualizing compartments using quite large bin sizes (>>1 kb).  Our experiments have nothing to do with the large-scale compartments seen in these Hi-C experiments.  Instead, we are studying the properties of individual TADs: how TADs are formed, the relationship between TAD topology and boundary:boundary pairing, and the impact of TAD topology on interactions between TADs in the immediate neighborhood.  There is no evidence to date that these large compartments or “block polymer co-segregation” have a) any impact on the properties of individual boundary elements, b) have a role in determining which boundary elements actually come together to form a given TAD, c) impact the orientation of the interactions between boundaries that generate the TAD or d) determine how TADs tend to interact with their immediate neighbors.  

In more recent publications (c.f., Harris et al. 2023) compartments have shrunk in size and instead of being units of several hundred kb, the median length of the “compartmental” unit in mammalian cells is about12 kb. This is not too much different from the size of fly TADs.  However, the available evidence does not support the idea that block polymer co-segregation/co-repulsion drive the TAD:TAD interactions seen in MicroC experiments.  For example, according to this “micro-compartment” model, the specific patterns of interaction between TADs in the CG3294 meta-loop in Author response image 3 would be driven by block polymer co-segregation and co-repulsion. In this model, the TAD upstream of the blue boundary (which contains CG33543, the odorant binding protein gene Obp22a and the Npc2a gene which encodes a protein involved in sterol homeostasis) would share the same chromatin state/biophysical properties as the TAD upstream of the purple boundary, which has the fipi gene. While it is true that CG33543, Obp22a and also the fipi gene are not expressed in embryos, Npc2a is expressed at high levels during embryogenesis, yet it is part of the TAD that interacts with the fipi TAD.  The TAD downstream of the blue boundary contains CG15353 and Nplp4 and it interacts with the TAD downstream of the purple boundary which contains CG3294 and slf.  CG15353 and Nplp4 are not expressed in the embryo and as such should share a compartment with a TAD that is also silent. However, slf is expressed at a high level in 1216 hr embryos, while CG3294 is expressed at a low level.  In neither case would one conclude that the TADs upstream and downstream of the blue and purple boundaries, respectively, interact because of shared chromatin/biophysical states that drive block polymer co-segregation corepulsion.