Author response:

Reviewer #1 - Public Review

This report describes work aiming to delineate multi-modal MRI correlates of psychopathology from a large cohort of children of 9-11 years from the ABCD cohort. While uni-modal characterisations have been made, the authors rightly argue that multi-modal approaches in imaging are vital to comprehensively and robustly capture modes of large-scale brain variation that may be associated with pathology. The primary analysis integrates structural and resting-state functional data, while post-hoc analyses on subsamples incorporate task and diffusion data. Five latent components (LCs) are identified, with the first three, corresponding to p-factor, internal/externalising, and neurodevelopmental Michelini Factors, described in detail. In addition, associations of these components with primary and secondary RSFC functional gradients were identified, and LCs were validated in a replication sample via assessment of correlations of loadings.

1.1) This work is clearly novel and a comprehensive study of associations within this dataset. Multi-modal analyses are challenging to perform, but this work is methodologically rigorous, with careful implementation of discovery and replication assessments, and primary and exploratory analyses. The ABCD dataset is large, and behavioural and MRI protocols seem appropriate and extensive enough for this study. The study lays out comprehensive associations between MRI brain measures and behaviour that appear to recapitulate the established hierarchical structure of psychopathology.

We thank Reviewer 1 for appreciating our methods and findings, and we address their suggestions below:

1.2) The work does have weaknesses, some of them acknowledged. There is limited focus on the strength of observed associations. While the latent component loadings seem reliably reproducible in the behavourial domain, this is considerably less the case in the imaging modalities. A considerable proportion of statistical results focuses on spatial associations in loadings between modalities - it seems likely that these reflect intrinsic correlations between modalities, rather than associations specific to any latent component.

We appreciate the Reviewer’s comment, and minimized the reporting of correlations between the loadings from the different modalities in the revised Results (specifically subsections on LC1, LC2, and LC3). We now refer to Table S4 in each subsection for this information: “Spatial correlations between modality-specific loadings are reported in Supplementary file 1c.”

For completeness, we report the intrinsic correlations between the different modalities in Supplementary file 1c (P.19):

“Lastly, although the current work aimed to reduce intrinsic correlations between variables within a given modality through running a PCA before the PLS approach, intrinsic correlations between measures and modalities may potentially be a remaining factor influencing the PLS solution. We, thus, provided an additional overview of the intrinsic correlations between the different neuroimaging data modalities in the supporting results (Supplementary file 1c).”

1.3) Assessment of associations with functional gradients is similarly a little hard to interpret. Thus, it is hard to judge the implications for our understanding of the neurophysiological basis of psychopathology and the ability of MRI to provide clinical tools for, say, stratification.

We now provide additional context, including a rising body of theoretical and empirical work, that outlines the value of functional gradients and cortical hierarchies in the understanding of brain development and psychopathology. Please see P.26.

“Initially demonstrated at the level of intrinsic functional connectivity (Margulies et al., 2016), follow up work confirmed a similar cortical patterning using microarchitectural in-vivo MRI indices related to cortical myelination (Burt et al., 2018; Huntenburg et al., 2017; Paquola et al., 2019), post-mortem cytoarchitecture (Goulas et al., 2018; Paquola et al., 2020, 2019), or post-mortem microarray gene expression (Burt et al., 2018). Spatiotemporal patterns in the formation and maturation of large-scale networks have been found to follow a similar sensory-to-association axis; moreover, there is the emerging view that this framework may offer key insights into brain plasticity and susceptibility to psychopathology (Sydnor et al., 2021). In particular, the increased vulnerability of transmodal association cortices in late childhood and early adolescence has been suggested to relate to prolonged maturation and potential for plastic reconfigurations of these systems (Paquola et al., 2019; Park et al., 2022b). Between mid-childhood and early adolescence, heteromodal association systems such as the default network become progressively more integrated among distant regions, while being more differentiated from spatially adjacent systems, paralleling the development of cognitive control, as well as increasingly abstract and logical thinking. [...] This suggests that neurodevelopmental difficulties might be related to alterations in various processes underpinned by sensory and association regions, as well as the macroscale balance and hierarchy of these systems, in line with previous findings in several neurodevelopmental conditions, including autism, schizophrenia, as well as epilepsy, showing a decreased differentiation between the two anchors of this gradient (Hong et al., 2019). In future work, it will be important to evaluate these tools for diagnostics and population stratification. In particular, the compact and low dimensional perspective of gradients may provide beneficial in terms of biomarker reliability as well as phenotypic prediction, as previously demonstrated using typically developing cohorts (Hong et al. 2020) On the other hand, it will be of interest to explore in how far alterations in connectivity along sensory-to-transmodal hierarchies provide sufficient graduality to differentiate between specific psychopathologies, or whether they, as the current work suggests, mainly reflect risk for general psychopathology and atypical development.”

1.4) The observation of a recapitulation of psychopathology hierarchy may be somewhat undermined by the relatively modest strength of the components in the imaging domain.

We thank the Reviewer for this comment, and now expressed this limitation in the revised Discussion, P.23.

“The p factor, internalizing, externalizing, and neurodevelopmental dimensions were each associated with distinct morphological and intrinsic functional connectivity signatures, although these relationships varied in strength.”

1.5) The task fMRI was assessed with a fairly basic functional connectivity approach, not using task timings to more specifically extract network responses.

In the revised Discussion on P.24, we acknowledge that more in-depth analyses of task-based fMRI may have offered additional insights into state-dependent changes in functional architecture.

“While the current work derived main imaging signatures from resting-state fMRI as well as grey matter morphometry, we could nevertheless demonstrate associations to white matter architecture (derived from diffusion MRI tractography) and recover similar dimensions when using task-based fMRI connectivity. Despite subtle variations in the strength of observed associations, the latter finding provided additional support that the different behavioral dimensions of psychopathology more generally relate to alterations in functional connectivity. Given that task-based fMRI data offers numerous avenues for analytical exploration, our findings may motivate follow-up work assessing associations to network- and gradient-based response strength and timing with respect to external stimuli across different functional states.”

1.6) Overall, the authors achieve their aim to provide a detailed multimodal characterisation of MRI correlations of psychopathology. Code and data are available and well organised and should provide a valuable resource for researchers wanting to understand MRI-based neural correlates of psycho-pathology-related behavioural traits in this important age group. It is largely a descriptive study, with comparisons to previous uni-modal work, but without particularly strong testing of neuroscience hypotheses.

We thank the Reviewer for recognizing the detail and rigor of data-driven study and extensive code and data documentation.

Reviewer #2 - Public Review

In "Multi-modal Neural Correlates of Childhood Psychopathology" Krebets et al. integrate multi-modal neuroimaging data using machine learning to delineate dissociable links to diverse dimensions of psychopathology in the ABCD sample. This paper had numerous strengths including a superb use of a large resource dataset, appropriate analyses, beautiful visualizations, clear writing, and highly interpretable results from a data-driven analysis. Overall, I think it would certainly be of interest to a general readership. That being said, I do have several comments for the authors to consider.

We thank Dr Satterthwaite for the positive evaluation and helpful comments.

2.1) Out-of-sample testing: while the permutation testing procedure for the PLS is entirely appropriate, without out-of-sample testing the reported effect sizes are likely inflated.

As discussed in the editorial summary of essential revisions, we agree that out-of-sample prediction indeed provides stronger estimates of generalizability. We assess this by applying the PCA coefficients derived from the discovery cohort imaging data to the replication cohort imaging data. The resulting PCA scores and behavioral data were then z-scored using the mean and standard deviation of the replication cohort. The SVD weights derived from the discovery cohort were applied to the normalized replication cohort data to derive imaging and behavioral composite scores, which were used to recover the contribution of each imaging and behavioral variable to the LCs (i.e., loadings). Out-of-sample replicability of imaging (mean r=0.681, S.D.=0.131) and behavioral (mean r=0.948, S.D.=0.022) loadings was generally high across LCs 1-5. This analysis is reported in the revised manuscript (P.18).

“Generalizability of reported findings was also assessed by directly applying PCA coefficients and latent components weights from the PLS analysis performed in the discovery cohort to the replication sample data. Out-of-sample prediction was overall high across LCs1-5 for both imaging (mean r=0.681, S.D.=0.131) and behavioral (mean r=0.948, S.D.=0.022) loadings.”

2.2) Site/family structure: it was unclear how site/family structure were handled as covariates.

Only unrelated participants were included in discovery and replication samples (see P.6). The site variable was regressed out of the imaging and behavioral data prior to the PLS analysis using the residuals from a multiple linear model which also included age, age2, sex, and ethnicity. This is now clarified on P.29:

“Prior to the PLS analysis, effects of age, age2, sex, site, and ethnicity were regressed out from the behavioral and imaging data using a multiple linear regression to ensure that the LCs would not be driven by possible confounders (Kebets et al., 2021, 2019; Xia et al., 2018). The imaging and behavioral residuals of this procedure were input to the PLS analysis.”

2.3) Anatomical features: I was a bit surprised to see volume, surface area, and thickness all evaluated - and that there were several comments on the correspondence between the SA and volume in the results section. Given that cortical volume is simply a product of SA and CT (and mainly driven by SA), this result may be pre-required.

As suggested, we reduced the reporting of correlations between the loadings from the different modalities in the revised Results (specifically subsections on LC1, LC2, and LC3). Instead, we now refer to Table S4 in each subsection for this information: “Spatial correlations between modality-specific loadings are reported in Supplementary file 1c.”

We also reran the PLS analysis while only including thickness and surface area as our structural metrics, to account for potential redundancy of these measures with volume. This analysis and associated findings are reported on P.36 and P.19:

“As cortical volume is a result of both thickness and surface area, we repeated our main PLS analysis while excluding cortical volume from our imaging metrics and report the consistency of these findings with our main model.”

“Third, to account for redundancy within structural imaging metrics included in our main PLS model (i.e., cortical volume is a result of both thickness and surface area), we also repeated our main analysis while excluding cortical volume from our imaging metrics. Findings were very similar to those in our main analysis, with an average absolute correlation of 0.898±0.114 across imaging composite scores of LCs 1-5.”

2.4) Ethnicity: the rationale for regressing ethnicity from the data was unclear and may conflict with current best practices.

We thank the Reviewer for this comment. In light of recent discussions on including this covariate in large datasets such as ABCD (e.g., Saragosa-Harris et al., 2022), we elaborate on our rationale for including this variable in our model in the revised manuscript on P.30:

“Of note, the inclusion of ethnicity as a covariate in imaging studies has been recently called into question. In the present study, we included this variable in our main model as a proxy for social inequalities relating to race and ethnicity alongside biological factors (age, sex) with documented effects on brain organization and neurodevelopmental symptomatology queried in the CBCL.”

We also assess the replicability of our analyses when removing race and ethnicity covariates prior to computing the PLS analysis and correlating imaging and behavioral composite scores across both models. We report resulting correlations in the revised manuscript (P.37, 19, and 27):

“We also assessed the replicability of our findings when removing race and ethnicity covariates prior to computing the PLS analysis and correlating imaging and behavioral composite scores across both models.”

“Moreover, repeating the PLS analysis while excluding this variable as a model covariate yielded overall similar imaging and behavioral composites scores across LCs to our original analysis. Across LCs 1-5, the average absolute correlations reached r=0.636±0.248 for imaging composite scores, and r=0.715±0.269 for behavioral composite scores. Removing these covariates seemed to exert stronger effects on LC3 and LC4 for both imaging and behavior, as lower correlations across models were specifically observed for these components.”

“Although we could consider some socio-demographic variables and proxies of social inequalities relating to race and ethnicity as covariates in our main model, the relationship of these social factors to structural and functional brain phenotypes remains to be established with more targeted analyses.”

2.5) Data quality: the authors did an admirable job in controlling for data quality in the analyses of functional connectivity data. However, it is unclear if a comparable measure of data quality was used for the T1/dMRI analyses. This likely will result in inflated effect sizes in some cases; it has the potential to reduce sensitivity to real effects.

We agree that data quality was not accounted for in our analysis of T1w- and diffusion-derived metrics. We now accounted for T1w image quality by adding manual quality control ratings to the regressors applied to all structural imaging metrics prior to performing the PLS analysis, and reported the consistency of this new model with original findings. See P.36, P.19:

“We also considered manual quality control ratings as a measure of T1w scan quality. This metric was included as a covariate in a multiple linear regression model accounting for potential confounds in the structural imaging data, in addition to age, age2, sex, site, ethnicity, ICV, and total surface area. Downstream PLS results were then benchmarked against those obtained from our main model.”

“Considering scan quality in T1w-derived metrics (from manual quality control ratings) yielded similar results to our main analysis, with an average correlation of 0.986±0.014 across imaging composite scores.”

As for diffusion imaging, we also regressed out effects of head motion in addition to age, age2, sex, site, and ethnicity from FA and MD measures and reported the consistency with our original results (P.36, P.19):

“We tested another model which additionally included head motion parameters as regressors in our analyses of FA and MD measures, and assessed the consistency of findings from both models.”

“Additionally considering head motion parameters from diffusion imaging metrics in our model yielded consistent results to those in our main analyses (mean r=0.891, S.D.=0.103; r=0.733-0.998).”

Reviewer #3 - Public Review

In this study, the authors utilized the Adolescent Brain Cognitive Development dataset to investigate the relationship between structural and functional brain network patterns and dimensions of psychopathology. They identified multiple components, including a general psychopathology (p) factor that exhibited a strong association with multimodal imaging features. The connectivity signatures associated with the p factor and neurodevelopmental dimensions aligned with the sensory-to-transmodal axis of cortical organization, which is linked to complex cognition and psychopathology risk. The findings were consistent across two separate subsamples and remained robust when accounting for variations in analytical parameters, thus contributing to a better understanding of the biological mechanisms underlying psychopathology dimensions and offering potential brain-based vulnerability markers.

3.1) An intriguing aspect of this study is the integration of multiple neuroimaging modalities, combining structural and functional measures, to comprehensively assess the covariance with various symptom combinations. This approach provides a multidimensional understanding of the risk patterns associated with mental illness development.

We thank the Reviewer for acknowledging the multimodal approach, and for the constructive suggestions.

3.2) The paper delves deeper into established behavioral latent variables such as the p factor, internalizing, externalizing, and neurodevelopmental dimensions, revealing their distinct associations with morphological and intrinsic functional connectivity signatures. This sheds light on the neurobiological underpinnings of these dimensions.

We are happy to hear the Reviewer appreciates the gain in understanding neural underpinnings of dimensions of psychopathology resulting from the current work.

3.3) The robustness of the findings is a notable strength, as they were validated in a separate replication sample and remained consistent even when accounting for different parameter variations in the analysis methodology. This reinforces the generalizability and reliability of the results.

We appreciate that the Reviewer found our robustness and generalizability assessment convincing.

3.4) Based on their findings, the authors suggest that the observed variations in resting-state functional connectivity may indicate shared neurobiological substrates specific to certain symptoms. However, it should be noted that differences in resting-state connectivity between groups can stem from various factors, as highlighted in the existing literature. For instance, discrepancies in the interpretation of instructions during the resting state scan can influence the results. Hence, while their findings may indicate biological distinctions, they could also reflect differences in behavior.

For the ABCD dataset, resting-state fMRI scans were based on eyes open and passive viewing of a crosshair, and are thus homogenized. We acknowledge, however, that there may still be state-to-state fluctuations contributing to the findings, and this is now discussed in the revised Discussion, on P.28. Note, however, that prior literature has generally also suggested rather modest impacts of cognitive and daily variation on resting-state functional networks, compared to much more dominating inter-individual and inter-group factors.

“Finally, while prior research has shown that resting-state fMRI networks may be affected by differences in instructions and study paradigm (e.g., with respect to eyes open vs closed) (Agcaoglu et al., 2019), the resting-state fMRI paradigm is homogenized in the ABCD study to be passive viewing of a centrally presented fixation cross. It is nevertheless possible that there were slight variations in compliance and instructions that contributed to differences in associated functional architecture. Notably, however, there is a mounting literature based on high-definition fMRI acquisitions suggesting that functional networks are mainly dominated by common organizational principles and stable individual features, with substantially more modest contributions from task-state variability (Gratton et al. 2018). These findings, thus, suggest that resting-state fMRI markers can serve as powerful phenotypes of psychiatric conditions, and potential biomarkers (Abraham et al., 2017; Gratton et al., 2020; Parkes et al., 2020).”

3.5) The authors conducted several analyses to investigate the relationship between imaging loadings associated with latent components and the principal functional gradient. They found several associations between principal gradient scores and both within- and between-network resting-state functional connectivity (RSFC) loadings. Assessing the analysis presented here proves challenging due to the nature of relating loadings, which are partly based on the RSFC, to gradients derived from RSFC. Consequently, a certain level of correlation between these two variables would be expected, making it difficult to determine the significance of the authors' findings. It would be more intriguing if a direct correlation between the composite scores reflecting behavior and the gradients were to yield statistically significant results.

We thank the Reviewer for the comment, and agree that investigating gradient-behavior relationships could offer additional insights into the neural basis of psychiatric symptomatology. However, the current analysis pipeline precludes this direct comparison which is performed on a region-by-region basis across the span of the cortical gradient. Indeed, the behavioral loadings are provided for each CBCL item, and not cortical regions.

The Reviewer also evokes concerns of potential circularity in our analysis, as we compared imaging loadings, which are partially based on RSFC, and gradient values generated from the same RSFC data. In response to this comment, we cross-validated our findings using an RSFC gradient derived from an independent dataset (HCP), showing highly consistent findings to those presented in the manuscript. This correlation is now reported in the Results section P.15.

“A similar pattern of findings was observed when cross-validating between- and within-network RSFC loadings to a RSFC gradient derived from an independent dataset (HCP), with strongest correlations seen for between-network RSFC loadings for LC1 and LC3 (LC1: r=0.50, pspin<0.001; LC3: r=0.37, pspin<0.001).”

We furthermore note similar correlations between imaging loadings and T1w/T2w ratio in the same participants, a proxy of intracortical microstructure and hierarchy (Glasser et al., 2011). These findings are now detailed in the revised Results, P.15-16:

“Of note, we obtain similar correlations when using T1w/T2w ratio in the same participants, a proxy of intracortical microstructure and hierarchy (Glasser et al., 2011). Specifically, we observed the strongest association between this microstructural marker of the cortical hierarchy and between-network RSFC loadings related to LC1 (r=-0.43, pspin<0.001).”

3.6) Lastly, regarding the interpretation of the first identified latent component, I have some reservations. Upon examining the loadings, it appears that LC1 primarily reflects impulse control issues rather than representing a comprehensive p-factor. Furthermore, it is worth noting that within the field, there is an ongoing debate concerning the interpretation and utilization of the p-factor. An insightful publication on this topic is "The p factor is the sum of its parts, for now" (Fried et al, 2021), which explains that the p-factor emerges as a result of a positive manifold, but it does not necessarily provide insights into the underlying mechanisms that generated the data.

We thank the Reviewer for this comment, and added greater nuance into the discussion of the association to the p factor. We furthermore discuss some of the ongoing debate about the use of the p factor, and cite the recommended publication on P.27.

“Other factors have also been suggested to impact the development of psychopathology, such as executive functioning deficits, earlier pubertal timing, negative life events (Brieant et al., 2021), maternal depression, or psychological factors (e.g., low effortful control, high neuroticism, negative affectivity). Inclusion of such data could also help to add further mechanistic insights into the rather synoptic proxy measure of the p factor itself (Fried et al., 2021), and to potentially assess shared and unique effects of the p factor vis-à-vis highly correlated measures of impulse control.”

This passage highlights Sita’s duty as a wife to share her husband’s fate and accompany him in exile. She argues that a wife must share with her husband. Rama’s fate, as she cannot find refuge or protection from anyone else but him. Throughout the Book, Rama tries to dissuade by describing the difficulties and horrors of the wilderness; however, Sita emphasizes that her love and commitment transcend fear and discomfort while emphasizing that her happiness stems from being benign with him rather than living in luxury. Sita’s speech simultaneously highlights the traditional gender roles and stereotypical expectations placed on both men and women. The idea of a ‘hero’ is identified with masculinity and being warrior-like (physical toughness). Sita refers to Rama as the ‘best of heroes’ and dismisses the idea of leaving the hand as suggesting that it would be "unworthy of a warrior's fame" and bring "shame" to a "monarch's son." This emphasizes the societal expectation that a hero must uphold his honor and strength, particularly in the context of his relationships and duties. Additionally, Sita's declaration that "the wife alone, whate'er await, must share on earth her husband's fate" underscores the patriarchal norm that a woman's place is with her husband, highlighting her role as a devoted and submissive partner. This builds on the cultural- and somewhat universal- stereotype that a woman’s role, as a wife, heavily resides in her being a devoted and submissive partner to her husband. When comparing different translations and adaptations of the Ramayana, variations in the portrayal of gender roles can be observed. For instance, in some modern adaptations, there may be a subtle shift towards portraying Sita with more agency and independence, reflecting contemporary views on gender equality. However, in traditional versions, such as those by Valmiki and other ancient translators, the patriarchal mindset is more pronounced. Yet, Sita's role is predominantly defined by her loyalty and subservience to Rama. The language used to describe Rama and Sita's roles reflects the societal norms and expectations of the time. Phrases such as "unworthy of a warrior's fame" and "the wife alone, whate'er await, must share on earth her husband's fate" reveal the deeply ingrained gender roles and the emphasis on male heroism and female subservience. However, the linguistic value of the work also lies in its expressive qualities as Sita’s heart-touching lines: "through tangled thorn and matted grass," illustrate the depth of her love for Rama. Ultimately, the translations differ based on the politics of the time and culture. CC BY Aarushi Attray (contact)

Valmiki. The Ramayana. Translated by Ralph T.H. Griffith, Project Gutenberg, 2009, Book II: Canto XXVII.: Sítá’s Speech, https://sacred-texts.com/hin/rama/ry105.htm. Accessed 4 Aug. 2024.

Valmiki. The Ramayana of Valmiki. Translated by Hari Prasad Shastri, Shanti Sadan, 1952.

Giwe's unwavering loyalty and honor for Kay-Khosrow is admirable and shows why he is well respected. He sacrifices his own life for Kay and does his best to convince him on why his survival is important for the better of the kingdom. This shows the importance of leadership and why Giwe is willing to sacrifice himself because he knows that the empire will not be successful without a good leader in place. His selflessness is also inspiring for a lot of readers as people tend to forget that being selfless can be admirable. As humans, we want the attention and credit for achievements so to see someone else give up their pride for a larger cause, it is very admirable and encourages other people to do the same in similar situations. Similar to Giwe, there are people on the frontlines and in war who put themselves out there for a similar reason as they want to protect the people in their country and are fighting for something much bigger than themselves. While not everyone is fighting for something bigger than them, Giwe reminds us to work for something bigger than us and to have a positive impact on other people because that is what we should do as people. Not to mention, Kay-Khosrow is successful in enacting revenge over Afrasiyab showing that good will always triumph over evil and continuing the legacy of his father. CC BY Ajey Sasimugunthan (contact)

Kay-Khosrow coming to find out his true heritage is an interesting moment because there is so much internal conflict as he is young and now is confused about his upbringing. He has come to express his own dissatisfaction with his simple upbringing despite being from loyalty and is now told the truth. The feeling must be bittersweet because he knows the truth on one hand but feels like he must have been lied to for his entire life. He feels a disconnect between his lowly origins in comparison to the elevated treatment he can get now being of royalty. It is similar to the feeling someone must feel if they are told that they were adopted later in life. They feel like they lose a part of themselves as they think they are not true members of the family and face a lot of internal conflict about their upbringing and why they were lied to for such a long time. The reference of "son of a shepherd" is what allows the readers to understand that he had a simple life growing up which is why it must feel out of place for him to be associated with royalty. An interesting theme that this brings up is the idea of social status and how that plays into someone's personal identity. People are judged by the social status they belong in so it must be an interesting transition for him to move up social status where he will be treated more favorably as well. It raises the question as to why people in higher social status gets to be treated better when all people should inherently be treated equally. CC BY Ajey Sasimugunthan (contact)

Reviewer #1 (Public Review):

Summary:

Using a mouse model of head and neck cancer, Barr et al show that tumor-infiltrating nerves connect to brain regions via the ipsilateral trigeminal ganglion, and they demonstrate the effect this has on behavior. The authors show that there are neurites surrounding the tumors using a WGA assay and show that the brain regions that are involved in this tumor-containing circuit have elevated Fos and FosB expression and increased calcium response. Behaviorally, tumor-bearing mice have decreased nest building and wheel running and increased anhedonia. The behavior, Fos expression, and heightened calcium activity were all decreased in tumor-bearing mice following nociceptor neuron elimination.

Strengths:

This paper establishes that sensory neurons innervate head and neck cancers and that these tumors impact select brain areas. This paper also establishes that behavior is altered following these tumors and that drugs to treat pain restore some but not all of the behavior. The results from the experiments (predominantly gene and protein expression assays, cFos expression, and calcium imaging) support their behavioral findings both with and without drug treatment.

Comments on previously identified weaknesses:

The authors have addressed the majority of my concerns.

Reviewer #2 (Public Review):

Summary:

Cancer treatments are not just about the tumor - there is an ever-increasing need for treating pain, fatigue, and anhedonia resulting from the disease as patients are undergoing successful but prolonged bouts with cancer. Using an implantable oral tumor model in the mouse, Barr et al describe neural infiltration of tumors, and posit that these nerve fibers are transmitting pain and other sensory signals to the brain that reduce pleasure and motivation. These findings are in part supported by anatomical and transcriptional changes in the tumor that suggest sensory innervation, neural tracing, and neural activity measurements. Further, the authors conduct behavior assays in tumor-bearing animals and inhibit/ablate pain sensory neurons to suggest involvement of local sensory innervation of tumors in mediating cancer-induced malaise.

Strengths:

• This is an important area of research that may have implications for improving the quality of life of cancer patients.

• The studies use a combination of approaches (tracing and anatomy, transcriptional, neural activity recordings, behavior assays, loss-of-function) to support their claims.

• Tracing experiments suggest that tumor-innervating afferents are connected to brain nuclei involved in oral pain sensing. Consistent with this, the authors observed increased neural activity in those brain areas of tumor-bearing animals. It should be noted that some of these brain nuclei have also been implicated in cancer-induced behavioral alterations in non-head and neck tumor models.

• Experiments are well-controlled and approaches are validated.

• The paper is well-written and the layout was easy to follow.

Weaknesses/Future Directions:

• The main claim is that tumor-infiltrating nerves underlie cancer-induced behavioral alterations. While the studies are supportive of this conclusion, manipulations in the current study are non-specific, ablating all TRPV1 sensory neurons. A direct test would be to selectively inhibit/ablate nerve fibers innervating the tumor or mouth region.

Author response:

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

Public Reviews:

Reviewer #1:

(1) Study suggests that the effects of their tumor models of mouse behavioral are largely non-specific to the tumor as most behaviors are rescued by analgesic treatment. So, most of the changes were likely due to site-specific pain and not a unique signal from the tumor.

The tumor generates pain at the site it is implanted, and it is likely amplified by the oral activities tumor bearing mice have to engage in. As there is no pain in the absence of the tumor, the pain is, by definition, caused by the tumor, not by the site. Concerning the relationship between pain and behavior, the behavioral assays undertaken in our study (nesting, cookie test, wheel running) were very limited in scope.  Two of these assays (nesting, cookie test) require use of the oral cavity. Only nesting and wheel running were assessed in the context of treatment for pain. Nesting behavior was completely restored with carprofen and buprenorphine treatment suggesting that in the absence of pain, mice were able to make perfect nests. Consistent with this, carprofen and buprenorphine treated animals also gained weight indicating that eating (another activity dependent on the oral cavity) was also restored.  Wheel running, an activity that does not rely on the oral cavity, was only partially restored with drug treatment. While additional behavioral tests are necessary to confirm this finding, the data suggest that there is pain-independent information relayed to the brain which accounts for this decline in wheel running.

Reviewer #2:

(1) The main claim is that tumor-infiltrating nerves underlie cancer-induced behavioral alterations, but the experimental interventions are not specific enough to support this. For example, all TRPV1 neurons, including those innervating the skin and internal organs, are ablated to examine sensory innervation of the tumor. Within the context of cancer, behavioral changes may be due to systemic inflammation, which may alter TRPV1 afferents outside the local proximity of tumor cells. A direct test of the claims of this paper would be to selectively inhibit/ablate nerve fibers innervating the tumor or mouth region.

We agree with the reviewer that a direct test of the hypothesis would require selectively inhibiting the nerve fibers innervating the tumor and assessing the impact on behavior. Studies in the lab are on-going using pharmacological interventions to do this. These studies are beyond the scope of this current manuscript.

(2) Behavioral results from TRPV1 neuron ablation studies are in part confounded by differing tumor sizes in ablated versus control mice. Are the differences in behavior potentially explained by the ablated animals having significantly smaller tumors? The differences in tumor sizes are not negligible. One way to examine this possibility might be to correlate behavioral outcomes with tumor size.

As suggested by the reviewer, we have graphed nesting scores and time-to-interact (cookie test) relative to tumor volume.  In both cases, we used simple linear regression to fit the data and analyzed the slopes of the lines. In the case of nesting, there was no significant difference between the slopes. This is now included as Supplemental Figure 4A. In the case of the cookie test, there was a significant difference between the slopes. This is now included as Supplemental Figure 4B. Graphing the data in this way allows one to look at any given tumor volume and infer what the nesting score and the time-to-interact for the two groups of mice. The linear regression model fits the time to interact with the cookie reasonably well, thus from this graph, we can see that at any given tumor volume the time to interact with the cookie was generally shorter in TRPV1cre::DTAfl/wt animals as compared to C57BL/6 mice. Unfortunately, the linear regression does not fit the nesting data very well and thus it is more difficult to make the comparison of tumor volume and nesting score.

The following text has been added to the results section.

Given the impact of nociceptor neuron ablation on tumor growth, we wondered whether differences in tumor volume contributed to the behavioral differences we noted. Thus, the behavior data were graphed as a function of tumor volume (Supplemental Fig 4A, B). A simple linear regression model was used to fit the data. In the case of nesting scores, the linear regression did not fit the data points very well making it difficult to assess nesting scores at a given tumor volume (Supplemental Fig 4A). However, the linear regression model fit the time to interact data better. Here, the graph suggests that tumor volume did not influence behavior as at any given tumor volume the time to interact with the cookie is generally smaller in TRPV1-Cre::Floxed-DTA animals as compared to C57BL/6 animals (Supplemental Fig 4B).

Reviewer #3:

(1) The authors mention in their Discussion the need for additional experiments. Could they also include / comment on the potential impact on the anti-tumor immune system in their model?

The following text has been added to the discussion:

Neuro-immune interactions have been studied in the context of a variety of conditions including, but not limited to infection 109, inflammation 110,111, homeostasis in the gut 112-114, as well as neurological diseases115,116. Neuro-immune communications in the context of cancer and behavior have also been studied (e.g., sickness behavior, depression) 117-119 however, these studies did not assess these interactions at the tumor bed. Investigations into neuro-immune interactions occurring within primary malignancies which harbor nerves have shed light on these critical communications. In the context of melanoma, which is innervated by sensory nerves, we identified that release of the neuropeptide calcitonin gene related peptide (CGRP) induces immune suppression. This effect is mediated by CGRP binding to its receptor, RAMP1, which is expressed on CD8+ T cells 49. A study utilizing a different syngeneic model of oral cancer similarly found an immune suppressive role for CGRP 120-122. These studies demonstrate that neuro-immune interactions occur at the tumor bed. Our current findings indicating that tumor-infiltrating nerves connect to a circuit that includes regions within the brain suggest that neuro-immune interactions within the peripheral malignancy may contribute to the behavioral alterations we studied.

(2) The authors mention the importance of inflammation contributing to pain in cancer but do not clearly highlight how this may play a role in their model. Can this be clarified?

The following text has been added to the discussion section of the manuscript.

Moreover, given that carprofen and buprenorphine decrease inflammation 104, their ability to restore normal nesting and cookie test behaviors (which require the use of the oral cavity where the tumor is located) suggests that inflammation at the tumor site contributed to the decline in these behaviors in vehicle-treated animals. Since both drugs were given systemically and each only partially restored wheel running, it suggests that systemic inflammation alone cannot fully account for the decline in wheel running seen in vehicle-treated animals. We posit that the inflammation- and pain-independent component of this behavioral decline is mediated via the transcriptional and functional alterations in the cancer-brain circuit.

(3) The tumor model apparently requires isoflurane injection prior to tumor growth measurements. This is different from most other transplantable types of tumors used in the literature. Was this treatment also given to control (i.e., non-tumor) mice at the same time points? If not, can the authors comment on the impact of isoflurane (if any) in their model?

Mice in all groups (tumor and non-tumor) were treated with isoflurane. This important detail has been added to the methods section.

(4) The authors emphasize in several places that this is a male mouse model. They mention this as a limitation in the Discussion. Was there an original reason why they only tested male mice?

The following text has been added in the discussion section:

Head and neck cancer is predominantly a cancer in males; it occurs in males three times more often than in females 123, this disparity increases in certain parts of the world. While smoking cigarettes and drinking alcohol are risk factors for HPV negative head and neck squamous cell carcinoma, even males that do not smoke and drink are have a higher susceptibility for this cancer than females 124,125. Thus, our studies used only male mice. However, we do recognize that females also get this cancer. In fact, female patients with head and neck cancer, particularly oral cancer, report more pain than their male counterparts 126,127. These findings suggest that differences in tumor innervation exist in males and females.

Therefore, another project in the lab has been to compare disease characteristics (including innervation and behavior) in male and female mice. The findings from this second study are the topic of a separate manuscript.

Recommendations For The Authors:

Reviewing editor:

(1) Tumors can communicate with the brain via blood-borne agents from the tumor itself or immune cells that are activated by the tumor in addition to neurons that invade the tumor. The xia and malaise that accompanies some tumors can be mediated by direct innervation and/or the humoral factors because both can activate the same parabrachial pathway. This paper makes the case for the direct innervation being important but ignores the possibility of both being involved. The interesting observation that innervation supports tumor growth (perhaps via substance P) is troublesome because the slower appearance of behavioral consequences (Figures 4 & 5) could be attributed to the smaller tumor size. A nice control for humoral effects would be to implant the tumor cells someplace in the body where innervation does not occur (if possible) and then examine behavioral outcomes.

In the course of several projects, we have implanted different tumor cell lines in different locations in mice (oral cavity, hind limb, flank, peritoneal cavity). In each location, tumor innervation occurs. This is not a phenomenon found only in mice as we completed an immunohistological survey of human cancers from different sites and found they are all innervated (PMID 34944001). These data are consistent with tumor and locally-released factors that recruit nerves to the tumor bed (PMID: 30327461)(PMID: 32051587)(PMID: 27989802). Thus, an implantation site that does not result in tumor innervation is currently unknown and likely does not exist.

(2) The authors should address whether there is an inflammatory component in this tumor model.

MOC2-7 tumors have been characterized as non-inflamed and poorly immunogenic 129-131.

This information has been added to the methods section.

(3) The RTX experiment in Figure 5 would be more compelling if the drug was injected directly into the tumor rather than injecting it in the flank, thus ablating all TRPV1-exressing neurons as in the genetic approach.

While we agree with the reviewer that ablating the TRPV1-expressing neurons at the tumor site directly would be ideal, RTX treatment takes approximately one week for ablation to occur but a significant amount of inflammation is associated with this. Therefore, we wait a total of 4 weeks for the inflammation to resolve. By this time, tumors have generally reached sacrifice criteria. Thus, this approach would not enable the question to be answered Moreover, we are not aware of any studies in which RTX has been injected in the oral cavity or face. While RTX is utilized clinically to treat pain, it is typically administered intrathecally, epidurally or intra-ganglionically (PMID: 37894723).

(4) The authors address affective aspects of pain but do not adequately address the sensory aspects, e.g., sensitivity to touch, heat and/or cold. They attribute the decrease in food disappearance (consumption) and nest building to oral pain, but it could be due to anhedonia and anorexia that can accompany tumor progression.

Assaying for touch and heat/cold sensitivity in the oral cavity is a critical aspect of studying head and neck cancer that needs to be addressed. However, in rodents these assays are not trivial given that any touch/heat/cold in the area of the tumor (oral cavity) impacts the sensitive whiskers in that region which directly influence these assays. Thus, we have been refining assays (e.g., OPAD, facial von Frey) to address these important questions. The findings from these studies are beyond the scope of this manuscript.

The reviewer makes a good point about anhedonia and anorexia. The following text has been added to the results section:

Pain-induced anhedonia is mediated by changes in the reward pathway. Specifically, in the context of pain, dopaminergic neurons in the ventral tegmental area (VTA) become less responsive to pain and release less serotonin.  This decreased serotonin results in disinhibition of GABA release; the resulting increased GABA promotes an increased inhibitory drive leading to anhedonia  82 and, when extreme, anorexia. Carprofen and buprenorphine treatments completely reversed nesting behavior and significantly improved eating. Inflammation 83 and opioids 84 directly influence reward processing and though our tracing studies did not indicate that the tumor-brain circuit includes the VTA, this brain region may be indirectly impacted by tumor-induced pain in the oral cavity. Thus, an alternative interpretation of the data is that the effects of carprofen and buprenorphine treatments on nesting and food consumption may be due to inhibition of anhedonia (and anorexia) rather than, or in addition to, relieving oral pain.

(5) Comment on why only males were used in this study.

Please see response to public reviews.

Reviewer #1:

(1) Please provide a justification for the use of exclusively male mice and expand in the discussion if there is potential for these findings to be directly applicable to female mice as well.

Please see response to public reviews.

The following text has been added to the discussion:

Head and neck cancer is predominantly a cancer in males; it occurs in males three times more often than in females 123, this disparity increases in certain parts of the world. While smoking cigarettes and drinking alcohol are risk factors for HPV negative head and neck squamous cell carcinoma, even males that do not smoke and drink are have a higher susceptibility for this cancer than females 124,125. Thus, our studies used only male mice. However, we do recognize that females also get this cancer. In fact, female patients with head and neck cancer, particularly oral cancer, report more pain than their male counterparts 126,127. These findings suggest that differences in tumor innervation exist in males and females.

(2) When discussing the results shown in Figure 2, please include some mention of Fus, since it was the highest expressed transcript.

The following text has been added to the results section regarding Fus.

The gene demonstrating the highest increase in expression, Fus, was of particular interest; it increases in expression within DRG neurons following nerve injury and contributes to injury-induced pain 51,52. Of note, we purposefully used whole trigeminal ganglia rather than FACS-sorted tracer-positive dissociated neurons to avoid artificially imposing injury and altering the transcript levels of these cells 53,54. Thus, significantly elevated expression of Fus by ipsilateral TGM neurons from tumor-bearing animals suggests the presence of neuronal injury induced by the malignancy. This is consistent with our previous findings 55 and those of others 56 showing that tumor-infiltrating nerves harbor higher expression of nerve-injury transcripts and neuronal sensitization.

(3) In line 197 please clarify the mice used. Were all mice tumor-bearing and some had nociceptors ablated, or was there a control (no tumor) group as well?

Line 197 refers to Figure 4D. In this figure, panels B-D show quantification of cFos and DFosB in the spinal nucleus of the TGM (SpVc), The parabrachial nucleus (PBN) and the Central nucleus of the amygdala (CeA). These data are from C57BL/6 and TRPV1cre::DTAfl/wt animals all of whom had tumor. Supplementary Figure 3C also show quantification of cFos and DFosB but these are from control, non-tumor bearing animals. The fact that controls are non-tumor-bearing has been added to the supplemental figure legend and the text of the results section has been clarified as follows.

While Fos expression was similar between non-tumor bearing mice of the two genotypes (Supplemental Fig. 3C-E), the absence of nociceptor neurons in tumor-bearing animals decreases cFos and DFosB in the PBN, and DFosB in the SpVc (Fig. 4B, C).

(4) Overall it would improve the readability of the figures if the colors for the IHC channels were on the image itself and not exclusively in the figure legend.

The colors for all the staining have been added to each panel.

(5) It is not a problem that complete cartography was not done, but please include a justification for why the brain regions that were focused on were chosen.

In order to ensure that our neural tracing technique captured only nerves present within the tumor bed, we restricted the injection of tracer to only 2 µl. We demonstrated that this small volume did not leak out of the tumor (Figure 1) and thus any tracer labeled neurons we identified were deemed as being connected in a circuit to nerves in the tumor bed. While we acknowledged that this calculated technical approach restricted our ability to tracer label all neurons in the tumor bed (as well as those they share circuitry with), it ensured no tracer leakage and inadvertent labeling of non-tumoral nerves. In non-tumor animals injected with 10 µl of tracer, labeled regions in the brain included the spinal nucleus of the trigeminal, the parabrachial nucleus, the central amygdala, the facial nucleus and the motor nucleus of the trigeminal. The regions that were tracer positive when tumor was injected were limited to the spinal nucleus of the trigeminal, the parabrachial nucleus and the central amygdala. Thus, the regions in the brain that we focused on were the areas that became tracer-positive following injection of tracer into the tumor.

(6) Were the cells that were injected cultured in media with 10% fetal calf serum? If so was any inflammatory response seen? If not please state in the methods section the media that cells for injection were cultured in.

The cells injected into animals were cultured in media containing 10% fetal calf serum. When cells are harvested for tumor injections, they are first washed two times with PBS and then trypsinized to detach the cells from the plate. Cells are collected, washed again with PBS and resuspended with DMEM without serum; this is what is injected into animals. We harvest cells in this way in order to eliminate any serum being injected into mice. This information has been added to the Methods section.

(7) Would any of the differences in drug treatment (Carprofen vs Buprenorphine) be due to the differing routes of administration and metabolism of the drugs?

Since carprofen and buprenorphine each resulted in similar behavioral impacts (nesting and wheel running), their different routes of administration seem to play a minor or no role in the behaviors assessed.

(8) Please include in the methods section the specific approach and software that was used for processing calcium imaging data and calculating a relative change in fluorescence.

The specific approach used for processing calcium imaging data and calculating relative change in fluorescence as well as the software used are all included in the methods section. Please see below:

Ca2+ imaging. TGM neurons from non-tumor and tumor-bearing animals (n=4-6 mice/condition) were imaged on the same day. Neurons were incubated with the calcium indicator, Fluo-4AM, at 37°C for 20 min. After dye loading, the cells were washed, and Live Cell Imaging Solution (Thermo-Fisher) with 20 mM glucose was added. Calcium imaging was conducted at room temperature. Changes in intracellular Ca2+ were measured using a Nikon scanning confocal microscope with a 10x objective. Fluo-4AM was excited at 488 nm using an argon laser with intensity attenuated to 1%. The fluorescence images were acquired in the confocal frame (1024 × 1024 pixels) scan mode. After 1 min of baseline measure, capsaicin (300nM final concentration) was added. Ca2+ images were recorded before, during and after capsaicin application. Image acquisition and analysis were achieved using NIS-Elements imaging software. Fluo-4AM responses were standardized and shown as percent change from the initial frame. Data are presented as the relative change in fluorescence (DF/F0), where F0 is the basal fluorescence and DF=F-F0 with F being the measured intensity recorded during the experiment. Calcium responses were analyzed only for neurons responding to ionomycin (10 µM, positive control) to ensure neuronal health. Treatment with the cell permeable Ca2+ chelator, BAPTA (200 µM), served as a negative control.

(9) Suggestions for Figure 1:

- In Figures 1C, D, E, include labels for the days of tumor harvest.

- Please make the size of the labels the same for 1K an 1L and align them.

- Microscopy image in Figure 1L for SpVc looks like it may be at a different magnification.

- If possible, include (either in the figure or the supplement) IHC images staining for Dcx and tau, which would complement the western blot data.

The requested changes to the figures have been made. Unfortunately, we do not have Dcx and tau IHC staining of the day 4, 10 and 20 tumors.

(10) Suggestions for Figure 2:

- Include directly onto the graph in Figure 2a the legend for tumor-bearing (red) and non-tumor bearing (blue).

- Keep consistent between Figure 2G and 2H/I if the tumor/nontumor will be labeled as T/N or Tumor/Control.

The requested changes to the figures have been made.

(11) Suggestions for Figure 3:

- An example trace of calcium signal would complement Figure 3G, H well.

Example tracings of calcium signal are already provided in Supplementary Figure 3A and B.

Reviewer #2:

(1) While the use of male mice is acknowledged, there is not a rationale for why female mice were not included in the study.

Please see the response to Reviewer #1 (first question).

(2) Criteria for euthanasia should be described in the Methods. This is especially needed for interpreting the survival curve in Figure 4H.

Criteria for euthanasia in our IACUC approved protocol include:

- maximum tumor volume of 1000mm3

- edema

- extended period of weight loss progressing to emaciation

- impaired mobility or lesions interfering with eating, drinking or ambulation

- rapid weight loss (>20% in 1 week)

- weight loss at or more than 20% of baseline

In addition to tumor size and weight loss, we use the body condition score to evaluate the state of animals and to determine euthanasia.  These details have been added to the Methods section.

(3) At what stage in cancer progression were the Fos studies conducted for Figure 4A-D?

The brains used for Fos staining (Fig 4B-D) were harvested at week 5 post-tumor implantation.

(4) For Fos counts, what are the bregma coordinates for the sections that were quantified?

SpVc:  -7.56 to -8.24mm

PBN:  -4.96 to -5.52mm

CeA:  -0.82mm to -1.94mm

(5) Statistics are needed for the claim in Lines 171-173.

The statistical analysis of Fos staining from tumor-bearing and non-tumor bearing brains are included in Figure 3D-F. The statistical analysis of ex vivo Ca+2 imaging of brains from tumor-bearing and non-tumor bearing animals are included in Figure 3 I and J.

(6) How long was the baseline period for weight and food intake measurements? How long were the animals single-housed before taking the baseline measurements?  

Baseline weight and food intake measurements were 2 weeks and animals were singly housed before baseline measurements for 2 weeks (a total of 4 weeks).

Minor:

(7) The authors might consider rewording the sentence on lines 59-62, given that it is abundantly clear from rodent studies that both the tumor and chemotherapy are associated with adverse behavioral outcomes.

We have reworded the sentence as follows:  The association of cancer with impaired mental health is directly mediated by the disease, its treatment or both; these findings suggest that the development of a tumor alters brain functions.

(8) Line 212 needs a space between the two sentences.

This has been fixed.

(9) Font size in Figure 2 is not consistent with the other figures.

This has been fixed.

(10) "DAPI" is the more conventional than "DaPi".

This has been fixed.

Editorial Comments and Suggestions:

(1) The Abstract would be better if it were more concise, e.g. ~175 words.

The abstract has been shortened as requested and now reads:

Cancer patients often experience changes in mental health, prompting an exploration into whether nerves infiltrating tumors contribute to these alterations by impacting brain functions. Using a mouse model for head and neck cancer and neuronal tracing we show that tumor-infiltrating nerves connect to distinct brain areas. The activation of this neuronal circuitry altered behaviors (decreased nest-building, increased latency to eat a cookie, and reduced wheel running). Tumor-infiltrating nociceptor neurons exhibited heightened calcium activity and brain regions receiving these neural projections showed elevated cFos and delta FosB as well as increased calcium responses compared to non-tumor-bearing counterparts. The genetic elimination of nociceptor neurons decreased brain Fos expression and mitigated the behavioral alterations induced by the presence of the tumor. While analgesic treatment restored nesting and cookie test behaviors, it did not fully restore voluntary wheel running indicating that pain is not the exclusive driver of such behavioral shifts. Unraveling the interaction between the tumor, infiltrating nerves, and the brain is pivotal to developing targeted interventions to alleviate the mental health burdens associated with cancer.

(2) Lines 28, 104, 258, 486, 521, and many other places, "utilized" should be "used" because the former refers to an application for which it is not intended, e.g. a hammer was utilized as a doorstop.

The requested changes have been made.

(3) Lines 32 and 73, it is not clear whether the basal activity is heightened or whether excitability is increased. "manifest" might be better than "harbor" on line 73.

We have changed the wording in the abstract to be clearer. Moreover, our finding that TGM neurons from tumor-bearing animals have increased expression of the s1-Receptor and phosphorylated TRPV1 (Fig 2G-I) indicate that these neurons have increased excitability.

(4) Line 34 and elsewhere, it would be better to refer to Fos because the is no need to distinguish cellular, cFos, from viral, vFos, in this context.

The requested changes have been made.

(5) Line 38, It would be better to refer to what was actually measured rather than "oral movements".

The requested changes have been made. The sentence now reads: “While analgesic treatment restored nesting and cookie test behaviors, it did not fully restore voluntary wheel running.”

(6) Line 84, CXCR3-null mouse on a C57BL/6 background.

The requested change has been made.

(7) Lines 86,129 wild-type, male mice.

The requested change has been made.

(8) Lines114-115, the brackets are not necessary.

The requested change has been made.

(9) Lines 118, 384, 409, 527, 589, 971, 974 always leave a space between numbers and units. Use Greek u for micro.

The requested change has been made.

(10) Lines 123-124, it is not clear that there is meaningful labeling within the CeA.

We have replaced this image with a more representative one of the CeA from a tumor-bearing animal with clear tracer labeling.

(11) Lines 125, 138, and 246 transcription was not measured, only transcript levels were measured.

The requested changes have been made.

(12) Line 133, I think >4 fold is meant.

Thank you for catching that. I have fixed it to >4 fold.

(13) Line 165, single-time-point assessment (add hyphens).

The requested change has been made.

(14) Line 181 and elsewhere including figure, the superscripts refer to alleles of the genes; hence approved gene names should be used in italics (as in Methods), TRPV1-Cre:: Floxed-DTA (without italics) would be acceptable.

The requested changes have been made.

(15) Line 182, nociceptor-neuron-ablated mice (add hyphens).

The requested changes have been made.

(16) Line 197, It is not clear that the "speed" of food disappearance was measured or that it is due to oral pain vs loss of appetite.

The reviewer makes a good point. We have changed the sentence to read:

To evaluate the effects of this disruption on cancer-induced behavioral changes, we assessed the animals’ general well-being through nesting behavior 32 and anhedonia using the cookie test 76,77, as well as  body weight and food disappearance as surrogates for oral pain and/or loss of appetite.

(17) Line 199, The reduced tumor growth after ablation could account for most of the changes in the other parameters that were measured.

We have graphed the nesting scores and time-to-interact with the cookie as a function of tumor volume.  These data are now included as Supplemental Figure 4 and suggest that at the same tumor volume, nesting scores and times-to-interact with the cookie are different between the groups.

(18) Line 204 TPVP1 spelling. Is the TGN smaller after ablation of half of the neurons?

The requested change has been made.

(19) Line 235, "now" is not necessary.

The requested change has been made.

(20) Line 238-239 and elsewhere, a few references for to why the TGN-SpVc-PBN-CeA circuit is relevant would be helpful.

The following references have been added regarding the relevance of this circuit to behavior:

Molecular Brain 14: 94 (2021) (PMID 34167570)

Neuropharmacology 198: 108757 (2021) (PMID 34461068)

Frontiers in Cellular Neuroscience 16: 997360 (2022)  (PMID 36385947)

Neuropsychopharmacology  49(3): 508-520 (2024) (PMID 37542159)

(21) Lines 371, 434 and Figures, gm should be g or grams in scientific usage. Include JAX lab stock numbers for these mouse lines.

The requested changes have been made.

(22) Line 432, removing food for one hour is not a fast.

The sentence has been reworded as follows: One hour prior to testing, mouse food is removed and the animals are acclimated to the brightly lit testing room.

(23) Line 476, 5-um sections (add hyphen).

The hyphen has been added.

(24) Lines 988, and 1023, DAPI are usually shown this way.

The requested change has been made.

(25) Figure 1K, add Bregma levels to figures.

SpVc: -8.12 mm

PBN: -5.34 mm

CeA: -1.34 mm

(26) Figure 3 line 1033, "area under the curve" What curve was examined?

The curve examined was the change in fluorescence over time. This curve has been added as Supplemental Figure 3C.

(27) Figure 3B, the circled area is the lateral PBN. At first glance, I thought scp was meant as the label for the circled area.

Scp is noted in the figure legend as a landmark.

What evidence is provided to suggest that it was intentionally unsecure?

Way to flip the argument on its head. In other words: (I guess?) "You should have known a much larger violent mob was coming, and therefore you should have increased the police presence more?"

This argument is pure madness. It's arguing that the blame for the capitol being overrun isn't the actual crowd itself, or perhaps the president who urged them all to show up, but rather with those in charge of the response who failed to grasp how extreme it was going to get.

Orwellian.

She's citing the president? That's hardly objective.

There's a story on him here. But where is the evidence that he was actually a "fed" as opposed to just a garden variety Trump supporter?

But Disney decided not to let that happen.

Reviewer #2 (Public Review):

Cuevas et al. investigate the stimulus selectivity of surround-induced responses in the mouse primary visual cortex (V1). While classical experiments in non-human primates and cats have generally demonstrated that stimuli in the surround receptive field (RF) of V1 neurons only modulate activity to stimuli presented in the center RF, without eliciting responses when presented in isolation, recent studies in mouse V1 have indicated the presence of purely surround-induced responses. These have been linked to prediction error signals. In this study, the authors build on these previous findings by systematically examining the stimulus selectivity of surround-induced responses.

Using neuropixels recordings in V1 and the dorsal lateral geniculate nucleus (dLGN) of head-fixed, awake mice, the authors presented various stimulus types (gratings, noise, surfaces) to the center and surround, as well as to the surround only, while also varying the size of the stimuli. Their results confirm the existence of surround-induced responses in mouse V1 neurons, demonstrating that these responses do not require spatial or temporal coherence across the surround, as would be expected if they were linked to prediction error signals. Instead, they suggest that surround-induced responses primarily reflect the representation of the achromatic surface itself.

The literature on center-surround effects in V1 is extensive and sometimes confusing, likely due to the use of different species, stimulus configurations, contrast levels, and stimulus sizes across different studies. It is plausible that surround modulation serves multiple functions depending on these parameters. Within this context, the study by Cuevas et al. makes a significant contribution by exploring the relationship between surround-induced responses in mouse V1 and stimulus statistics. The research is meticulously conducted and incorporates a wide range of experimental stimulus conditions, providing valuable new insights regarding center-surround interactions.

However, the current manuscript presents challenges in readability for both non-experts and experts. Some conclusions are difficult to follow or not clearly justified.

I recommend the following improvements to enhance clarity and comprehension:

(1) Clearly state the hypotheses being tested at the beginning of the manuscript.

(2) Always specify the species used in referenced studies to avoid confusion (esp. Introduction and Discussion).

(3) Briefly summarize the main findings at the beginning of each section to provide context.

(4) Clearly define important terms such as "surface stimulus" and "early vs. late stimulus period" to ensure understanding.

(5) Provide a rationale for each result section, explaining the significance of the findings.

(6) Offer a detailed explanation of why the results do not support the prediction error signal hypothesis but instead suggest an encoding of the achromatic surface.

These adjustments will help make the manuscript more accessible and its conclusions more compelling.

Is this a term that everyone would be familiar with? Because I'm not sure I could define it off the top of my head. I could hazard a pretty decent guess based on other similar words and the usage here, but...

Just off the top of my head, this feels potentially excessive. You should be able to narrow your focus down to just 1 or 2 that make the most sense for what you are trying to model.

This is less a comment about this paragraph and more the previous section:

This felt like a huge data analysis dump, and I was unable to keep most of it straight in my head and how exactly it was tied to your research question. There is a TON going on. At the end I have no clear indication what I should be taking away from it. I think you need to work on possibly trimming some of this away, and really fixating on a clear story, which you constantly relate back to.

Is this a term that everyone would be familiar with? Because I'm not sure I could define it off the top of my head. I could hazard a pretty decent guess based on other similar words and the usage here, but...

Just off the top of my head, this feels potentially excessive. You should be able to narrow your focus down to just 1 or 2 that make the most sense for what you are trying to model.

This is less a comment about this paragraph and more the previous section:

This felt like a huge data analysis dump, and I was unable to keep most of it straight in my head and how exactly it was tied to your research question. There is a TON going on. At the end I have no clear indication what I should be taking away from it. I think you need to work on possibly trimming some of this away, and really fixating on a clear story, which you constantly relate back to.

Jefferson wanted to change the structure of family, where men were the head of the household rather than women. In many Native American cultures, women were the head of the household, otherwise known as matriarchal.

8 colored boxes are 8 attention heads

Lennie seems like he takes a lot of pride in working hard. Was he ashamed that relying on public aid would disclose the fact that he was disabled?

noo don't leave him :(

guessing its gonna be howland just because of how recent it is

only ned has been able to kill in a single bloe (not counting payne)

ugh foreshadowing

I FEEL SO BAD FOR HIM AND ITS GONNA GET WORSE :(

poor girls :(

bloodraven?

eLife assessment

The authors have presented an interesting set of results showing that female sex peptide signaling adversely affects late-life neurodegeneration after early-life exposure to repetitive mild head injury in Drosophila. This fundamental work substantially advances our understanding of how sex-dependent response to TBI occurs by identifying the Sex Peptide and the immune system as modulators of sex differences. The evidence supporting the conclusions is compelling with rigorous inclusion of controls and appropriate statistics.

Reviewer #2 (Public Review):

Summary:<br /> In this manuscript, the authors use the Drosophila model system to study the impact of mild head trauma on sex-dependent brain deficits. They identify Sex Peptide as a modulator of greater negative outcomes in female flies. Additionally, they observe that increased age at the time of injury results in worse outcomes, especially in females, and that this is due to chronic suppression of innate immune defense networks in mated females. The results demonstrate a novel signaling pathway that promotes age- and sex-dependent outcomes after head injury.

Strengths:<br /> The authors have modified their previously reported TBI model in flies to mimic mild TBI, which is novel. Methods are explained in detail, allowing for reproducibility. Experiments are rigorous with appropriate statistics. A number if important controls are included. The work tells a complete mechanistic story and adds important data to increase our understanding of sex-dependent differences in recovery after TBI. The Discussion is comprehensive and puts the work in context of the field.

Weaknesses: None<br /> The authors answered the following concerns, and I have no other concerns:<br /> A very minor weakness is that exact n values should be included in the figure legends. There should also be confirmation of knockdown by RNAi in female flies either by immunohistochemistry or qRT-PCR if possible.

Reviewer #3 (Public Review):

Summary:<br /> In this manuscript, the authors used a Drosophila model to show that exposure to repetitive mild TBI causes neurodegenerative conditions that emerge late in life and disproportionately affect females. In addition to the well-known age-dependent impact, the authors identified Sex Peptide (SP) signaling as a key factor in female susceptibility to post-injury brain deficits.

Strengths:<br /> The authors have presented a compelling set of results showing that female sex peptide signaling adversely affects late-life neurodegeneration after early-life exposure to repetitive mild head injury in Drosophila. They have compared the phenotypes of adult male and female flies sustaining TBI at different ages, and the phenotypes of virgin females and mated females, 2) compared the phenotypes of eliminating SP signaling in mating females and introducing SP-signaling into virgin females, 3) compared transcriptomic changes of different groups in response to TBI. The results are generally consistent and robust.

Weaknesses:<br /> The authors have made their claims largely based on assaying climbing index and vacuole formation as the only indicators of late-life neurodegeneration after TBI. Furthermore, it is also really surprising to see so few DEGs even in wild-type males and mated females and to see that none of DEGs overlap among groups or are even related to the SP-signaling. The authors state that the reason is their TBI is very minor. It is critical to independently verify their RNA-sequencing results and to add some more molecular evidence to support their conclusion. Finally, since similar sex peptide signaling is not present in mammalians or humans, its implication in humans remains unclear.

Author response:

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

Reviewer #1 (Recommendations For The Authors):

My comments are largely limited to suggestions to make the manuscript easier to read and digest.

In the abstract they say RNA sequencing highlights changes in innate...

Could they be more specific? Innate immune system up or down? They do not indicate actual findings in the abstract.

We thank the reviewer for the comment and we have revised the abstract accordingly.  

Their use of non‐intuitive abbreviations is often confusing. Perhaps they can add a table in methods listing all the abbreviations so that the reader can follow the data better. mNGA, vmHT....etc.

As suggested, we have now included a list of the abbreviations used in the paper.

There are mis‐spellings in the manuscript.

We have gone through the manuscript and corrected the mis-spellings.   

Has the SPR RNAi line been validated?

The SPR RNAi line that we used has been extensively validated by Yapici et al., 2007 and several subsequent publications. Importantly, the effectiveness of SPR knockdown is evident in female flies as they exhibit dramatically reduced egg laying and, importantly, lack the typical post-mating behaviors (such as rejection of male flies after initial mating) observed in the wild type mated female flies. In fact, female flies with RNAi-mediated SPR knockdown behave identically to females mated with SP-null male flies, confirming the effective disruption of the SP-SPR signaling pathway. We have revised the manuscript and added these statements in the results section concerning SPR RNAi.  

In the figures showing the Climbing Index vs time, can they abbreviate seconds as sec vs s? At least I think it is seconds. At first, I thought it was Time or Times, and was confused about what they were indicating on those types of graphs (Figures 1D‐F).

We have revised the figure as suggested by the reviewer.

In Figure 3F, they have a significance indicated in an unclear manner. It looks like they are comparing neuropil to the cortex, but I think they really mean to compare the cortex of sham to cortex of D31?

The reviewer was correct. We have revised figure 3F to make this clear.     

In Figure 4B, what is the y‐axis? Percentage of what? Is that percentage of total flies?

The reviewer was correct. We have revised the figure to make this clear. 

In a figure like SF3 B, what is the y‐axis? "Norm. Accum. CI" Can they explain the abbreviation?

We have revised the Y-axis label to be “Normalized accumulative CI”.  We have also made this clear in the legend.   

In the methods, what does this mean: "Regions devoid of Hoechst and phalloidin signal in non‐physiologically appropriate areas were considered vacuoles"? What are non‐physiologically appropriate areas? To me, that would mean outside of the brain. I would have thought the areas should be physiologically appropriate (aka neuropil and cortex)? This is confusing.

We have revised the method section to be more specific.  In the Drosophila brain, there are structures such as esophagus that are devoid of both Hoechst and phalloidin staining, which were excluded from our vacuole quantification.    

Reviewer #2 (Recommendations For The Authors):

Since I use mammalian systems, my comment about the confirmation of siRNA should be removed if this is not possible in the Drosophila system.

We have revised the figures to include total N values when appropriate. Including individual n values for each experimental assay and condition will inevitably crowd the figure legends, so specific values are available upon request. 

Regarding RNAi knockdown of sex peptide receptors (SPRs), we agree that confirmation of the knockdown by IHC or qRT-PCR will further strengthen our findings. It should be noted, however, that the RNAi line we used has been extensively validated by Yapici et al., 2007 and several subsequent publications. Importantly, the effectiveness of SPR knockdown is evident in female flies as they exhibit dramatically reduced egg laying and, importantly, lack the typical post-mating behaviors (such as rejection of male flies after initial mating) observed in the wild type mated female flies. In fact, female flies with RNAi-mediated SPR knockdown behave identically to females mated with SP-null male flies, confirming the effective disruption of the SP-SPR signaling pathway. We have revised the manuscript to include these statements in the results concerning the SPR RNAi knockdown.    

Reviewer #3 (Recommendations For The Authors):

(1) In Figures 1 and 2, the authors found that females have a lower climbing index in the acute phase in D17 injury, not due to neurodegeneration as shown no significant changes of brain vacuolation and other markers. However, in Figure 3, the authors found that female flies have a lower climbing index, more brain vacuolation, and neurodegeneration in the late phase. It's not very convincing that having a lower climbing index at the late phase is due to neurodegeneration. Is it possible that females suffered from more severe acute effects, at least in D17 injury?

We thank the reviewer for this point. Female flies injured on D17 displayed acute climbing deficits at 90 minutes post-injury. Since we did not observe significant structural changes in the brain at this time, we believe that this short-term functional deficit is not due to acute neuronal death. Here it is important to note that males did not display any acute climbing deficits when injured on D17, which suggests that the females suffered from more severe acute effects than males. However, these injured female flies recovered fully at 24 hours post-injury and displayed no climbing deficits. At two weeks post-injury, we observe climbing deficits and increased vacuole formation as a direct result of the injuries on D17 (see Supplemental Figure 3). When we assessed sensorimotor behavior and brain vacuolation on D45, we found that the injured females had significantly lower climbing indices and more brain vacuolation than the non-injured females of the same age. In this case, the concurrent observance of decreased climbing ability and increased brain vacuolation suggests chronic neurodegeneration in aged, injured females. This is not to be confused with the acute neuronal death observed by other groups using injury models of stronger severity. Overall, our data are consistent with the current view that in many neurodegenerative diseases, functional deficits often precede observable brain degeneration, which may take years to manifest.

(2) The authors determined late‐life brain deficits and neurodegeneration purely based on climbing index and vacuole formation. These phenotypes are not really specific to TBI‐related neurodegeneration and the significance and mechanisms of vacuole formation are not clear. Indeed, in Figures 3 A and B, male flies especially D31inj tend to have a much larger variation than any other groups. What could be the reasons? The authors should perform additional analyses on TBI‐related neurodegeneration in flies, which have been shown before, such as retinal degeneration and loss, neuronal degeneration, and loss, neuromuscular junction abnormalities, etc (Genetics. 2015 Oct; 201(2): 377‐402).

We thank the reviewer for the thorough evaluation of our manuscript. The reviewer raised a very important question: whether the neurodegeneration observed in our model is specific to TBI. As the reviewer rightly pointed out, the neurodegenerative phenotypes are unlikely to be specific to TBI-related neurodegeneration. Throughout the manuscript, we have tried to convey the notion that the mild physical impacts to the head represent one form of environmental insults, which in combination with other risk factors such as aging can lead to the emergence of neurodegenerative conditions. It should be noted that the negative geotaxis assay and vacuolation quantification are two well-established approaches to assess sensorimotor deficits and frank brain degeneration in fly brains. 

It is important to emphasize that the head-specific impacts delivered to the flies in our study are much milder than those used in previous studies. As we showed in our figure 1, this very mild form of head trauma (referred to as vmHT) did not cause any death, nor affected the lifespan of the injured flies. Our supplemental data also show very minimal structural neuronal damage and no acute and chronic apoptosis induced by vmHT exposure. Consistently, we did not observe any exoskeletal or eye damage immediately following injuries, nor did we observe any retinal degeneration and pseudopupil loss at the chronic stage of these flies. We have incorporated these important points in the revised manuscript.  

(3) In Figure 4, it would be important to perform the behavior test fly speed and directional movement in the acute phase as well to determine whether the females have reduced performance at the acute phase.

We thank the reviewer for this suggestion. Please note that our modified NGA has already improved the spatiotemporal resolution over the classic NGA.  The data presented in Fig.3 show that there are no acute deficits for young cohorts.  Therefore, we do not believe that the detailed analysis of the direction and speed of these flies is essential.  

Unfortunately, the current setup for the AI-based analysis requires manual corrections of tracking errors, which are time-consuming and tedious.  We are building a newly designed AI-based NGA (NGA.ai) that will allow automatic tracking and quantification with minimal manual interventions. Once it is completed, we will perform some of the analyses that the reviewer suggested.  

(4) In Figure 8, the authors performed an RNA‐seq analysis and identified some dysregulated gene expressions. However, it is really surprising to see so few DEGs even in wild‐type males and mated females, and to see that none of DEGs overlap among groups or related to the SP‐signaling. This raises questions about the validity of the RNAseq analysis. It is critical to independently verify their RNA‐sequencing results and to add some more molecular evidence to support their conclusion.

We agree that future studies are needed to independently validate our RNA sequencing results. We believe that the small number of DEGs are likely due to two unique features of our study: (1) the very mild nature of our injury paradigm and (2) the chronic examination timepoint that was long after the head injury and SP exposure, which distinguish our study from previous fly TBI studies.  As pointed out in the manuscript, our study was aimed to understand how early life exposure to repetitive head traumatic insults could lead to the latelife onset of neurodegenerative conditions. We hope to further validate our results in our next phase of experiments using single-cell RNA sequencing and RT-qPCR. 

(5) The current results raise a series of interesting questions: what implication of female fly mating and its associated Sex Peptide signaling would be to mammalians or humans? Would mammalian female animals mating with wild‐type or sex hormone‐null male animals have different effects on their post‐injury behavior tests or neuropathological changes? What are the mechanisms underlying the sexual dimorphism?

As the reviewer pointed out, it would be very interesting to explore the possible roles of sex peptide-signaling in other animals and humans. As far as we know, there is no known mammalian ortholog to the insect sex peptide, so it would be difficult to study SP or an SPlike molecule in mammalian models. However, we believe that prolonged post-mating changes associated with reproduction in female fruit flies contribute to their elevated vulnerability to neurodegeneration.  In this regard, drastic changes within the biology of female mammals associated with reproduction can potentially lead to vulnerability to neurodegeneration. We agree that this demands further study, which may be done with future collaborators using rodent or large animal models.  We have discussed this point in the manuscript.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

Reply to the reviewers

Rebuttal_ Preprint- #RC-2023-02144

First of all we would like to thank the three reviewers for their constructive and positive comments and suggestions, and the time spent in reviewing our manuscript. Their suggestions and comments had contributed to improve our manuscript. We feel the manuscript is much strengthened by this revision.

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

__Summary:____ __The manuscript by Dabsan et al builds on earlier work of the Igbaria lab, who showed that ER-luminal chaperones can be refluxed into the cytosol (ERCYS) during ER stress, which constitutes a pro-survival pathway potentially used by cancer cells. In the current work, they extent these observations and a role for DNAJB12&14 in ERCYS. The work is interesting and the topic is novel and of great relevance for the proteostasis community. I have a number of technical comments:

We thank the reviewer for his/her positive comments on our manuscript.

__Major and minor comments: __

1- In the description of Figure 2, statistics is only show to compare untreated condition with those treated with Tg or Tm, but no comparison between condition and different proteins. As such, the statement made by the authors "...DNAJB14-silenced cells were only affected in AGR2 but not in DNAJB11 or HYOU1 cytosolic accumulation" cannot be made.

Answer: We totally agree with the reviewer#1. The aim of this figure is to show that during ER stress, a subset of ER proteins are refluxed to the cytosol. This is happening in cells expressing DNAJB12 and DNAJB14. We are not comparing the identity of the expelled proteins between DNAJB12-KD cells and DNAJB14-KD cells, This is not the scoop of this paper as such the statement was removed.

2- Figure S2C: D11 seems to increase in the cytosolic fraction after Tm and Tg treatment. However, this is not reflected in the text. The membrane fraction also increases in the DKO. Is the increase of D11 in both cytosol and membrane and indication for a transcriptional induction of this protein by Tm/Tg? Again, the authors are not reflecting on this in their text.

Answer: We performed qPCR experiments in control, DNAJB12-KD, DNAJB14-KD and in the DNAJB12/DNAJB14 double knock down cells (in both A549 and PC3 cells) to follow the mRNA levels of DNAJB11. As shown in (Figure S2F-S2N), there is no increase in the mRNA levels of DNAJB11, AGR2 or HYOU1 in the different cells in normal (unstressed conditions). Upon ER stress with tunicamycin or thapsigargin there is a little increase in the mRNA levels of HYOU1 and AGR2 but not in DNAJB11 mRNA levels. On the other hand, we also performed western blot analysis and we did not detect any difference between the different knockdown cells when we analyzed the levels of DNAJB11 compared to GAPDH. Those data are now added as (Figure S2F-S2N).

We must note that although AGR2 and HYOU1 are induced at the mRNA as a result of ER stress, the data with the overexpression of DNAJB12 and DNAJB14 are important as control experiments because when DNAJB12 is overexpressed it doesn’t inducing the ER stress (Figure S3C-S3D). In those conditions there is an increase of the cytosolic accumulation of AGR2, HYOU1 and DNAJB11 despite that there was no induction of AGR2, HYOU1 or DNAJB11 (Figure 3C and Figure 3E, Figure S3, Figure 4, and Figure S4) . Those results argue against the idea that the reflux is a result of protein induction and an increase in the total proteins levels.

3- Figure 2D: Only p21 is quantified. phospho-p53 and p53 levels are not quantified.

Answer: We added the quantification of phospho-p53 and the p53 levels to (Figure 2E-G). Additional blots of the P21, phosphor-p53 and p53 now added to FigureS2O.

4- Figure 2D: There appears to be a labelling error

Answer: Yes, the labelling error was corrected.

5- Are there conditions where DNAJB12 would be higher?

Answer: In some cancer types there is a higher DNAJB12, DNAJB14 and SGTA expression levels that are associated with poor prognosis and reduced survival (New Figure S6E-M). The following were added to the manuscript: “Finally, we tested the effect of DNAJB12, DNAJB14, and SGTA expression levels on the survival of cancer patients. A high copy number of DNAJB12 is an unfavorable marker in colorectal cancer and in head and neck cancer because it is associated with poor prognosis in those patients (Figure S6E). A high copy number of DNAJB12, DNAJB14, and SGTA is associated with poor prognosis in many other cancer types, including colon adenocarcinoma (COAD), acute myeloid leukemia (LAML), adrenocortical carcinoma (ACC), mesothelioma (MESO), and Pheochromocytoma and paraganglioma (PCPG) (Figure S6F-M). In uveal melanoma (UVM), a high copy number of the three tested genes, DNAJB12, DNAJB14, and SGTA, are associated with poor prognosis and poor survival (Figure S6I, S6J, and S6M). The high copy number of DNAJB12, DNAJB14, and SGTA is also associated with poor prognosis in many other cancer types but with low significant scores. More data is needed to make significant differences (TCGA database). We suggest that the high expression of DNAJB12/14 and SGTA in those cancer types may account for the poor prognosis by inducing ERCYS and inhibiting pro-apoptotic signaling, increasing cancer cells' fitness.

6- What do the authors mean by "just by mass action"?

Answer: Mass action means increasing the amount of the protein (overexpression). We corrected this in the main text to overexpression.

7- Figure 3C: Should be labelled to indicate membrane and cytosolic fraction. The AGR2 blot in the left part is not publication quality and should be replaced.

Answer: We added the labelling to indicate cytosolic and membrane fractions to Figure 3C. We re-blotted the AGR2, new blot of AGR2 was added.

8- What could be the reason for the fact that DNAJB12 is necessary and sufficient for ERCYS, while DNAJB14 is only necessary?

Answer: Because of their very high homology, we speculate that the two proteins have partial redundancy. Partial because we believe that some of the roles of DNAJB12 cannot be carried by DNAJB14 in its absence. Although they are highly homologous, we expect that they probably have different affinities in recruiting other factors that are necessary for the reflux of proteins.

We further developed around this point in the discussion and the main text.

9- Figure 5A: Is the interaction between SGTA and JB12 UPR-independent?HCS70 seems to show only background binding. The interaction of JB12 with SGTA is not convincing. A better blot is needed.

Answer: In the conditions of Figure 5A, we did not observe any induction of the UPR (Figure S3C-D). Thus, we concluded that in those condition of overexpression, DNAJB12 interacts with SGTA in UPR independent manner.

We repeated this experiment another 3 times with very high number of cells (2X15cm2 culture dishes for each condition) and instead of coimmunoprecipitating with DNAJB12 antibodies we IP-ed with FLAG-beads, the results are very clear as shown in the new Figure 5A compared to Figure S5A.

10- Figure 5B: the expression of DNAJB14 was induced by Tg50, but not by Tg25 or Tm. However, the authors have not commented on this. This should be mentioned in the text and discussed.

Answer: In most of the experiments we did not see an increase in DNAJB14 upon ER stress except in this replicate. To be sure we looked at the DNAJB14 levels upon ER stress by protein and qPCR experiment as shown in new (in the Input of Figure 5 and Figure S5) and (Figure S5H-I). We also added new IP experiments in Figure 5 and Figure S5.

11- Figure 6A: Why is a double knockdown important at all? DNAJB14 does not seem to do much at all (neither in overexpression nor with single knockdown).

Answer: the data shows that DNAJB12 can compensate for the lack of DNAJB14 while DNAJB14 can only partially compensate for some of the DNAJB12 functions. DNAJB12 could have higher affinity to recruit other factor needed for the reflux process and thus the impact of DNAJB12 is higher. In summary, neither DNAJB12 or DNAJB14 is essential in the single knockdown which means that they compensate for each other. In the overexpression experiment, it is enough to have the endogenous DNAJB14 for the DNAJB12 activity. When DNAJB14 is overexpressed at very high levels, we believe that it binds to some factors that are needed for proper DNAJB12 activity (Figure 4 showing that the WT-DNAJB14 inhibits ER-stress induced ER protein reflux when overexpressed). We believe that DNAJB14 is important because only when we knock both DNAJB12 and DNAJB14 we see an effect on the ER-protein reflux. DNAJB14 is part of a complex of DNAJB12/HSC70 and DSGTA.

(DNAJB12 is sufficient while DNAJB14 is not- please refer to point #8 above).

**Referees cross-commenting**

I agree with the comments raised by reviewer 1 about the manuscript. I also agree with the points written in this consultation session. In my opinion, the comments of reviewer 2 are phrased in a harsh tone and thus the reviewer reaches the conclusion that there are "serious" problems with this manuscript. However, I think that the authors could address many of the points of this reviewer in a matter of 3 months easily. For instance, it is easy to control for the expression levels of exogenous wild type and mutant D12 and compare it to the endogenous one (point 3). This is a very good point of this reviewer and I agree with this experiment. Likewise, it is easy to provide data about the levels of AGR2 to address the concern whether its synthesis is affected by D12 and D14 overexpression. Again, an excellent suggestion, but no reason for rejecting the story. As for not citing the literature, I think this can also easily be addressed and I am sure that this is just an oversight and no ill intention by the authors. __Overall, I am unable to see why the reviewer reaches such a negative verdict about this work. With proper revisions that might take 3 months, I think the points of all reviewers can be addressed. __

Reviewer #1 (Significance (Required)):

Significance: The strength of the work is that it provides further mechanistic insight into a novel cellular phenomenon (ERCYS). The functions for DNAJB12&14 are unprecedented and therefore of great interest for the proteostasis community. Potentially, the work is also of interest for cancer researchers, who might capitalize of the ERCYS to establish DNAJB12/14 as novel therapeutic targets. The major weaknesses are as follows: (i) the work is limited to a single cell line. To better probe the cancer relevance, the work should have used at least a panel of cell lines from one (or more) cancer entity. Ideally even data from patient derived samples would have been nice. Having said this, I also appreciate that the work is primarily in the field of cell biology and the cancer-centric work could be done by others. Certainly, the current work could inspire cancer specialists to explore the relevance of ERCYS. (ii) No physiological or pathological condition is shown where DNAJB12 is induced or depleted.

Answer: We previously showed that ERCYS is conserved in many different cell lines including A549, MCF7, GL-261, U87, HEK293T, MRC5 and others and is also conserved in murine models of GBM (GL-261 and U87 derived tumors) and human patients with GBM (Sicari et al. 2021). Here, we tested the reflux process and the IP experiments in many different cell lines including A549, MCF-7, PC3 and Trex-293 cells. We also added new fractionation experiment in DNAJB12 and DNAJB14 -depleted MCF-7, PC3 and A549 cells. We added all those data to the revised version.

We also added survival curves from the TCGA database showing that high copy number of DNAB12, DNAJB14 and SGTA are associated with poor prognosis compared to conditions where DNAJB12, DNAJB14, and SGTA are at low copy number (Figure S6E-M). Finally, we included immunofluorescent experiment to show that the interaction between the refluxed AGR2 and the cytosolic SGTA occurs in tumors collected from patients with colorectal cancer patients (Figure S5F-G) compared to non-cancerous tissue.

This study is highly significant and is relevant not only to cancer but for other pathways that may behave in similar manner. For instance, DNAJB12 and DNAJB14 are part of the mechanism that is used by non-envelope viruses to escape the ER to the cytosol. Thus, the role of those DNAJB proteins seems to be mainly in the reflux of functional (not misfolded) proteins from the ER to the cytosol. We reported earlier that the UDP-Glucose-Glucosyl Transferase 1 (UGGT1) is also expelled during ER stress. UGGT1 is important because it is redeploy to the cytosol during enterovirus A71 (EA71) infection to help viral RNA synthesis (Huang et al, 2017). This redeployment of EAA71 is similar to what happens during the reflux process because on one hand, UGGT1 exit the ER by an ER stress mediated process (Sicari et al. 2021) and it is also a functional in the cytosol as a proteins which help viral RNA synthesis ((Huang et al, 2017). All those data showing that there is more of DNAJB12, DNAJB14, DNAJC14, DNAJC30 and DNAJC18 that still needs to be explored in addition to what is published. Thus, we suggest that viruses hijacked this evolutionary conserved machinery and succeeded to use it in order to escape the ER to the cytosol in a manner that depends on all the component needed for ER protein reflux.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

The authors present a study in which they ascribe a role for a complex containing DNAJB12/14-Hsc70-SGTA in facilitating reflux of a AGR2 from the ER to cytosol during ER-stress. This function is proposed to inhibit wt-P53 during ER-stress.

Concerns: 1. The way the manuscript is written gives the impression that this is the first study about mammalian homologs of yeast HLJ1, while there are instead multiple published papers on mammalian orthologs of HLJ1. Section 1 and Figure 1 of the results section is redundant with a collection of previously published manuscripts and reviews. The lack of proper citation and discussion of previous literature prevents the reader from evaluating the results presented here, compared to those in the literature.

Answer: We highly appreciate the reviewer’s comments. This paper is not to show that DNAJB12 and DNAJB14 are the orthologues of HLJ-1 but rather to show that DNAJB12 and DNAJB14 are part of a mechanism that we recently discovered and called ERCYS that cause proteins to be refluxed out of the ER. A mechanism that is regulated in by HLJ-1 in yeast. ERCYS is an adaptive and pro-survival mechanism that results in increased chemoresistance and survival in cancer cells. The papers that reviewer #2 refer to are the ones that report DNAJB12 can replace some of the ER-Associated Degradation (ERAD) functions of HLJ-1 in degradation of membranal proteins such as CFTR. These two mechanism are totally different and the role of the yeast HLJ-1 in degradation of CFTR is not needed for ERCYS. This is because we previously showed that the role of the yeast HLJ-1 and probably its orthologues in ERCYS is independent of their activity in ERAD(Igbaria et al. 2019). Surprisingly, the role of HLJ-1 in refluxing the ER proteins is not only independent of the reported ERAD-functions of HLJ1 and the mammalian DNAJBs but rather proceeds more rigorously when the ERAD is crippled (Igbaria et al. 2019). This role of DNAJBs is unique in cancer cells and is responsible in regulating the activity of p53 during the treatment of DNA damage agents.

In our current manuscript we show by similarity, functionality, and topological orientation, that DNAJB12 and DNJB14 may be part of a well conserved mechanism to reflux proteins from the ER to the cytosol. A mechanism that is independent of DNAJB12/14’s reported activity in ERAD(Grove et al. 2011; Yamamoto et al. 2010; Youker et al. 2004). In addition, DNAJB12 and DNAJB14 facilitate the escape of non-envelope viruses from the ER to the cytosol in similar way to the reflux process(Goodwin et al. 2011; Igbaria et al. 2019; Sicari et al. 2021). All those data show that HLJ-1 reported function may be only the beginning of our understanding on the role that those orthologues carry and that are different from what is known about their ERAD function.

Action: We added the references to the main text and discussed the differences between the reported DNAJB12 and HLJ-1 functions to the function of DNAJB12, DNAJB14 and the other DNAJ proteins in the reflux process. We also developed around this in the discussion.

The conditions used to study DNAJB12 and DNAJ14 function in AGR2 reflux from the ER do not appear to be of physiological relevance. As seen below they involve two transfections and treatment with two cytotoxic drugs over a period of 42 hours. The assay for ERCY is accumulation of lumenal ER proteins in a cytosolic fraction. Yet, there is no data or controls that describe the path taken by AGR2 from the ER to cytosol. It seems like pleotropic damage to the ER due the experimental conditions and accompanying cell death could account for the reported results?

Transfection of cells with siRNA for DNAJB12 or DNAJB14 with a subsequent 24-hour growth period.

Transfection of cells with a p53-lucifease reporter.

Treatment of cells with etoposide for 2-hours to inhibit DNA synthesis and induce p53. D. Treatment of cells for 16 hours with tunicamycin to inhibit addition of N-linked glycans to secretory proteins and cause ER-stress.

Subcellular fractionation to determine the localization of AGR2, DNAJB11, and HYOU1

KD of DNAJB12 or DNAJB14 have modest if any impact on AGR2 accumulation in the cytosol. There is an effect of the double KD of DNAJB12 or DNAJB14 on AGR2 accumulation in the cytosol. Yet there are no western blots showing AGR2 levels in the different cells, so it is possible that AGR2 is not synthesized in cells lacking DNAJB12 and DNAKB14. The lack of controls showing the impact of single and double KD or DNAJB12 and DNAJB14 on cell viability and ER-homeostasis make it difficult to interpret the result presented. How many control versus siRNA KD cells survive the protocol used in these assays?

Answer: Despite the long protocol we see differences between the control cells and the DNAJB-silenced cells in terms of the quantity of the refluxed proteins to the cytosol. The luciferase construct was used to assess the activity of p53 so the step of the second transfection was used only in experiments were we assayed the p53-luciferase activity. The rest of the experiments especially those where we tested the levels of p53 and P21 levels, were performed with one transfection. Moreover, all the experiments with the subcellular protein fractionation were performed after one transfection without the second transfection of the p53-Luciferase reporter. Finally, the protocol of the subcellular protein fractionation requires first to trypsinize the cells to lift them up from the plates, at the time of the experiment the cells were almost at 70-80% confluency and in the right morphology under the microscope.

Here, we performed XTT assay and Caspase-3 assay to asses cell death at the end of the experiment and before the fractionation assay. We did not observe any differences at this stage between the different cell lines (Figure-RV1 for reviewers Only). This can be explained by the fact that we use low concentrations of Tm and Tg for short time of 16 hour after the pulse of etoposide.

Finally, the claim that and ER-membrane damage result in a mix between the ER and cytosolic components is not true for the following reasons: (1) In case of mixing we would expect that GAPDH levels in the membrane fraction will be increased and that we do not see, and (2) we used our previously described transmembrane-eroGFP (TM-eroGFP) that harbors a transmembrane domain and is attached to the ER membrane facing the ER lumen. The TM-eroGFP was found to be oxidized in all conditions tested. Those data argue against a rupture of the ER membrane which can results in a mix of the highly reducing cytosolic environment with the highly oxidizing ER environment by the passage of the tripeptide GSH from the cytosol to the ER. All those data argue against (1) cell death, and (2) rupture of the ER membrane. Figure RV1 Reviewers Only.

Moreover, as it is shown in Figure S2, AGR2 is found in the membrane fraction in all the four different knock downs, thus it is synthesized in all of them. Moreover, we assayed the mRNA levels of AGR2 in all the knockdowns and we so that they are at the same levels in all the 4 different conditions and still AGR2 mRNA levels increase upon ER stress in all of the 4 knockdown cells in different backgrounds (Figure S2F-N).

In Figure 3 the authors overexpress WT-D12 and H139Q-D12 and examine induction of the p53-reporter. There are no western blots showing the expression levels of WT-D12 and H139Q-D12 relative to endogenous DNAJB12. HLJ1 stands for high-copy lethal DnaJ1 as overexpression of HLJ1 kills yeast. The authors present no controls showing that WT-D12 and H139-D12 are not expressed at toxic levels, so the data presented is difficult to evaluate.

Answer: The expression levels of the overexpression of DNAJB12 and DNAJB14 were present in the initial submission of the manuscript as Figure S3A and S3B. The data showing the relationship between the expression degree and the viability were also included in the initial submission as Figure S3C (Now S3H).

There is no mechanistic data used to help explain the putative role DNAJB12 and DNAJB14 in ERCY? In Figure 4, why does H139Q JB12 prevent accumulation of AGR2 in the cytosol? There are no westerns showing the level to which DNAJB12 and DNAJB14 are overexpressed.

Answer: The data showing the levels of DNAJB12 compared to the endogenous were present in the initial submission as Figure S3A and S3B.

We suggest a mechanism by which DNAJB12 and DNAJB14 interact (Figure 5 and Figure S5) and oligomerize to expel those proteins in similar way to expelling non-envelope viruses to the cytosol. Thus, when expressing the mutant DNAJB12 H139Q may indicate that the J-domain dead-mutant can still be part of the complex but affects the J-domain activity in this oligomer and thus inhibit ER-protein reflux. In other words, we showed that the H139Q exhibits a dominant negative effect when overexpressed. Moreover, here we added another IP experiment in the D12/D14-DKD cells to show that in the absence of DNAJB12 and DNAJB14, SGTA cannot bind the ER-lumenal proteins because they are not refluxed (Figure 5 and Figure S5). Those data indicate that in order for SGTA bind the refluxed proteins they have to go through the DNAJB12 and DNAJB14 and their absence this interaction does not occur. This explanation was also present in the discussion of the initial submission.

Mechanistically, we show that AGR2 interacts with DNAJB12/14 which are necessary for its reflux. This mechanism involves the functionality of cytosolic HSP70 chaperones and their cochaperones (SGTA) proteins that are recruited by DNAJB12 and 14. This mechanism is conserved from yeast to mammals. Moreover, by using the alpha-fold prediction tools, we found that AGR2 is predicted to interact with SGTA in the cytosol by the interaction between the cysteines of SGTA and AGR2 in a redox-dependent manner.

**Referees cross-commenting**

__ __ I appreciate the comments of the other reviewers. I agree that the authors could revise the manuscript. Yet, based on my concerns about the physiological significance of the process under study and lack of scholarship in the original draft, I would not agree to review a revised version of the paper.

Answer: Regards the physiological relevance, we showed in our previous study (Sicari et al. 2021) how relevant is ERCYS in human patients of GBM and murine model of GBM. ERCYS is conserved from yeast to human and is constitutively active in GL-261 GBM model, U87 GBM model and human patients with GBM (Sicari et al. 2021). Here, extended that to other tumors and showed that DNAJB12, DNAJB14 and SGTA high levels are associated with poor prognosis in many cancer types (Figure S6). We also show some data from to show the relevance and added data showing the interaction of SGTA with AGR2 in CRC samples obtained from human patients compared to healthy tissue (Figure S5). This study is highly significant and is relevant not only to cancer but for other pathways that may behave in similar manner. For instance, DNAJB12 and DNAJB14 are part of the mechanism that is used by non-envelope viruses to escape the ER to the cytosol. Thus, the role of those DNAJB proteins seems to be mainly in the reflux of functional (not misfolded) proteins from the ER to the cytosol. We reported earlier that the UDP-Glucose-Glucosyl Transferase 1 (UGGT1) is also expelled during ER stress. UGGT1 is important because it is redeploy to the cytosol during enterovirus A71 (EA71) infection to help viral RNA synthesis (Huang et al, 2017). This redeployment of EAA71 is similar to what happens during the reflux process because on one hand, UGGT1 exit the ER by an ER stress mediated process (Sicari et al. 2021) and it is also a functional in the cytosol as a proteins which help viral RNA synthesis ((Huang et al, 2017). All those data showing that there is more of DNAJB12, DNAJB14, DNAJC14, DNAJC30 and DNAJC18 that still needs to be explored in addition to what is published. We suggest that viruses hijacked this evolutionary conserved machinery and succeeded to use it in order to escape.

We appreciate the time spent to review our paper and we are sorry that the reviewer reached such verdict that is also not understood by the other reviewers. Most of the points raised by reviewer 2 were already addressed and explained in the initial submission, anyways we appreciate the time and the comments of reviewer #2 on our manuscript.

Reviewer #2 (Significance (Required)):

Overall, there are serious concerns about the writing of this paper as it gives the impression that it is the first study on higher eukaryotic and mammalian homologs of yeast HLJ1. The reader is not given the ability to compare the presented data to related published work. There are also serious concerns about the quality of the data presented and the physiological significance of the process under study. In its present form, this work does not appear suitable for publication.

Answer: Again we thank reviewer #2 for giving us the opportunity to explain how significant is this manuscript especially for people who are less expert in this field. The significance of this paper (1) showing a the unique role of DNAJB12 and DNAJB14 in the molecular mechanism of the reflux process in mammalian cells (not their role in ERAD), (2) showing the implication of other cytosolic chaperones in the process including HSC70 and SGTA (3), our alpha-fold prediction show that this process may be redox dependent that implicate the cysteines of SGTA in extracting the ER proteins, (4) overexpression of the WT DNAJB12 is sufficient to drive this process, (5) mutation in the HPD motif prevent the reflux process probably by preventing the binding to the cytosolic chaperones, and (6) we need both DNAJB12 and DNAJB14 in order to make the interaction between the refluxed ER-proteins and the cytosolic chaperones occur.

In Summary, this study is highly significant in terms of physiology, we previously reported that ERCYS is conserved in mammalian cells and is constitutively active in human and murine tumors (Sicari et al. 2021). Moreover, DNAJB12 and DNAJB14 are part of the mechanism that is used by non-envelope viruses to escape the ER to the cytosol in a mechanism that is similar to reflux process (Goodwin et al. 2011; Goodwin et al. 2014). Thus, the role of those DNAJB proteins seems to be mainly in the reflux of functional proteins from the ER to the cytosol, viruses used this evolutionary conserved machinery and succeeded to use in order to escape. This paper does not deal with the functional orthologues of the HLJ-1 in ERAD but rather suggesting a mechanism by which soluble proteins exit the ER to the cytosol.

__Reviewer #3 (Evidence, reproducibility and clarity (Required)):____ __

Summary: Reflux of ER based proteins to the cytosol during ER stress inhibits wt-p53. This is a pro-survival mechanism during ER stress, but as ER stress is high in many cancers, it also promotes survival of cancer cells. Using A549 cells, Dabsan et al. demonstrate that this mechanism is conserved from yeast to mammalian cells, and identify DNAJB12 and DNAJB14 as putative mammalian orthologues of yeast HLJ1.

This paper shows that DNAJB12 and 14 are likely orthologues of HLJ1 based on their sequences, and their behaviour. The paper develops the pathway of ER-stress > protein reflux > cytosolic interactions > inhibition of p53. The authors demonstrate this nicely using knock downs of DNAJB12 and/or 14 that partially blocks protein reflux and p53 inhibition. Overexpression of WT DNAJB12, but not the J-domain inactive mutant, blocks etoposide-induced p53 activation (this is not replicated with DNAJB14) and ER-resident protein reflux. The authors then show that DNAJB12/14 interact with refluxed ER-resident proteins and cytosolic SGTA, which importantly, they show interacts with the ER-resident proteins AGR2, PRDX4 and DNAJB11. Finally, the authors show that inducing ER stress in cancer cell lines can increase proliferation (lost by etoposide treatment), and that this is partially dependent on DNAJB12/14.

This is a very interesting paper that describes a nice mechanism linking ER-stress to inhibition of p53 and thus survival in the face of ER-stress, which is a double edged sword regarding normal v cancerous cells. The data is normally good, but the conclusions drawn oversimplify the data that can be quite complex. The paper opens a lot of questions that the authors may want to develop in more detail (non-experimentally) to work on these areas in the future, or alternatively to develop experimentally and develop the observations further. There are only a few experimental comments that I make that I think should be done to publish this paper, to increase robustness of the work already here, the rest are optional for developing the paper further.

We thank the reviewer for his/her positive comments His/her comments contributed to make our manuscript stronger.

__Major comments:____ __

1. Number of experimental repeats must be mentioned in the figure legends. Figures and annotations need to be aligned properly

__Answer____: __All experiments were repeated at least 3 times. We added the number of repeats on each figure in the figures legends

Results section 2:

No intro to the proteins you've looked at for relocalization. Would be useful to have some info on why you chose AGR2. Apart from them being ER-localized, do they all share another common characteristic? Does ability to inhibit p53 vary in potency?

Answer: We previously showed that AGR2 is refluxed from the ER to the cytosol to bind and inhibit wt-p53 (Sicari et al. 2021). Here, we used AGR2 because, (1) we know that AGR2 is refluxed from the ER to the cytosol, and (2) we know which novel functions it gains in the cytosol so we are able to measure and provide a physiological significance of those novel functions when the levels of DNAJB12 and DNAJB14 are altered. Moreover, we used DNAJB11 (41 kDa) and HYOU1 (150 kDa) proteins to show that alteration in DNAJB12 or DNAJB14 prevent the reflux small, medium and large sized proteins. We added a sentence in the discussion stating that DNAJB12/14 are responsible for the reflux of ER-resident proteins independently of their size. We also added in the result section that we are looking at proteins of different sizes and activities.

What are the roles of DNAJB12/14 if overexpression can induce reflux? Does it allow increased binding of an already cytosolic protein, causing an overall increase in an interaction that then causes inhibition of p53? What are your suggested mechanisms?

Answer: Previously it was reported that over-expression of DNAJB12 and DNAJB14 tend to form membranous structures within cell nuclei, which was designate as DJANGOS for DNAJ-associated nuclear globular structures(Goodwin et al. 2014). Because those structures which contain both DNAJB12 and DNAJB14 also form on the ER membrane (Goodwin et al. 2014), we speculate that during stress DNAJB12/14 overexpression may facilitate ERCYS. Interestingly, those structures contain Hsc70 and markers of the ER lumen, the nuclear and ER and nuclear membranes (Goodwin et al. 2014).

The discussion was edited accordingly to further strengthen and clarify this point

Fig3: A+B show overexpression of individual DNAJs but not combined. As you go on to discuss the effect of the combination on AGR2 reflux, it would be useful to include this experimentally here.

Answer: This is a great idea, we tried to do it for long time. Unfortunately when we used cells overexpress DNAJB12 under the doxycycline promoter and transfect with DNAJB14 plasmid expressing DNAJB14 under the CMV promoter, most of the cells float within 24 hours compared to cells transfected with the empty vector alone or with DNAJB14-H136Q. We also did overexpression of DNAJB14 in cells with DNAJB12 conditional expression and also were lethal in Trex293T cells and A549-cells.

Fig 3C: Subfractionation of cells shows AGR2 in the cytosol of A549 cells. The quality of the data is good but the bands are very high on the blot. For publication is it possible to show this band more centralized so that we are sure that we are not missing bands cut off in the empty and H139Q lanes?

Also, you have some nice immunofluorescence in the 2021 EMBO reports paper, is it possible to show this by IF too? It is not essential for the story, but it would enrich the figure and support the biochemistry nicely. Also it is notable that the membrane fraction of the refluxed proteins doesn't appear to have a decrease in parallel (especially for AGR2). Is this because the % of the refluxed protein is very small? Is there a transcriptional increase of any of them (the treatments are 12+24 h so it would be enough time)? This could be a nice opportunity to discuss the amount of protein that is refluxed, whether this response is a huge emptying of the ER or more like a gentle release, and also the potency of the gain of function and effect on p53 vs the amount of protein refluxed. This latter part isn't essential but it would be a nice element to expand upon.

Answer: We re-blotted the AGR2 again, new blot of AGR2 was added. More blots also are added in Figure S2, the text is edited accordingly.

In new Figure S5 we added immunofluorescence experiment from tumors and non-tumors tissues obtained from Colorectal cancer (CRC) patients showing that the interaction between SGTA and the refluxed AGR2 also occurs in more physiological settings. It is also to emphasize that the suggested mechanism that implicates SGTA is also valid in CRC tumors.

We performed qPCR experiments in control, DNAJB12-KD, DNAJB14-KD and in the DNAJB12/DNAJB14 double knock down cells (in both A549 and PC3 cells) to follow the mRNA levels of DNAJB11. As shown in the Figure S2F-N, there is no increase in the mRNA levels of DNAJB11, AGR2 or HYOU1 in the different cells in normal (unstressed conditions). Upon ER stress with tunicamycin or thapsigargin there is a little increase in the mRNA levels of HYOU1 and AGR2 but in DNAJB11 mRNA levels. On the other hand, we also performed western blot analysis and we did not detect any difference between the different knockdown cells when we analyzed the levels of DNAJB11 compared to GAPDH. Those data are now added to Figure S2F-N. We must note that in AGR2 and HYOU1 are induced at the mRNA as a result of ER stress. The data with the overexpression of DNAJB12 and DNAJB14 are important control experiment where we show a reflux when DNAJB12 is overexpressed without inducing the ER stress (Figure 3, Figure 4, and Figure S3). In those conditions no induction of AGR2, HYOU1 or DNAJB11 were observed. Those results argue against the reflux as a result of protein induction and the increase in the proteins levels.

The overall protein levels in steady state are function of how much proteins are made, degraded and probably secreted outside the cell. We do see in Figure S2 under ER stress there are some differences in the levels of the mRNA, moreover, from our work in yeast we showed that the expelled proteins have very long half-life in the cytosol (Igbaria et al. 2019). Because it is difficult to assay how many of the mRNA is translated and how much of it is stable/degraded and the stability of the cytosolic fraction vs the ER, it is hard to interpret on the stability and the levels of the proteins.

Those data are now added to the manuscript, the text is edited accordingly.

You still mention DNAJB12 and 14 as orthologues, even though DNAJB14 has no effect on p53 activity when overexpressed. Do you think that this piece of data diminishes this statement?

Answer: The fact that DNAJB12 and DNAJB14 are highly homologous and that only the double knockdown has a great effect on the reflux process may indicate that they are redundant. Moreover, because only DNAJB12 is sufficient may indicate that some of DNAJB12 function cannot be carried by DNAJB14. In one hand they share common activities as shown in the double knock down and on the other hand DNAJB12 has a unique function that may not be compensated by DNAJB14 when overexpressed.

__ __ Fig 3D/F: Overexpression of DNAJB14 induces reflux of DNAJB11 at 24h, what does this suggest? Does this indicate having the same role as DNAJB12 but less potently? What's your hypothesis?

Answer: ERCYS is new and interesting phenomenon and the redistribution of proteins to the cytosol has been documented lately by many groups. Despite that we still do not know what is the specificity of DNAJB12 and DNAJB14 to the refluxed proteins. DNAJB11 is glycosylated protein and now we are testing whether other glycosylated proteins prefer the DNAJB14 pathway or not. This data is beyond the scope of this paper

"This suggests that the two proteins may have different functions when overexpressed, despite their overlapping and redundant functions" What does it suggest about their dependence on each other? If overexpression of WT DNAJB12 inhibits Tg induced reflux, is it also blocking the ability of DNAJB14 to permit flux?

Answer: We hypothesize that it is all about the stichometry and the ratios between proteins. When we overexpress DNAJB14 (the one that is not sufficient to cause reflux it may hijack common components and factor by non-specifically binding to them. Those factors may be needed for DNAJB12 to function properly (Like the dominant negative effect of the DNAJB12-HPD mutant for instance). On the other hand, DNAJB12 may have higher affinity for some cytosolic partner and thus can do the job when overexpressed. Here, we deal with the DNAJB12/DNAJB14 as essential components of the reflux process, yet we need to identify the interactome of each of the proteins during stress and the role of the other DNAJ proteins that also share some of the topological and structural similarity to DNAJB12, DNAJB14 and HLJ-1 (DNAJC30, DNAJC14, and DNAJC18). We edited the text accordingly and integrated this in the discussion.

__ __ Fig 4: PDI shown in blots but not commented on in text. Then included in the schematics. Please comment in the text.

Answer: We commented PDI in the text.

Fig 4F: Although the quantifications of the blots look fine, the blot shown does not convincingly demonstrate this data for AGR2. The other proteins look fine, but again it could be useful to see the individual means for each experiment, or the full gels for all replicates in a supplementary figure.

Answer: the other two repeats are in Figure S4

__ __Results section 3

Fig 5A, As there is obviously a difference between DNAJB12/14 it would be useful to do the pulldown with DNAJB14 too. Re. HSC70 binding to DNAJB12 and 14, the abstract states that DNAJB12/14 bind HSC70 and SGTA through their cytosolic J domains. Fig 5 shows pulldowns of DNAJB12 with an increased binding of SGTA in FLAG-DNAJB12 induced conditions, but the HSC70 band does not seem to be enriched in any of the conditions, including after DNAJB12 induction. This doesn't support the statement that DNAJB12 binds HSC70. In fact, in the absence of a good negative control, this would suggest that the HSC70 band seen is not specific. There is also no data to show that DNAJB14 binds HSC70. I recommend including a negative condition (ie beads only) and the data for DNAJB14 pulldown.

Answer: In Figure 5A we used the Flp-In T-REx-293 cells as it is easier to control and to tune up and down the expression levels of DNAJB12 and DNAJB14. According to new Figure S5A, DNAJB12 binds at the basal levels to HSC70 all the time. It was also surprising for us not to see the differences in the overexpression and we relate that to the fact that all the HSC70 are saturated with DNAJB12. In order to better assay that we repeated the IP in Figure 5A but instead of the IP with DNAJB12, we IP-ed with FLAG antibodies to selectively IP the transfected DNAJB12. As shown in the new Fig 5A, the increase of DNAJB12-FLAG is accompanied with an increase in the binding of HSC70.

We further tested the interaction between DNAJB12, DNAJB14 and HSC70 during ER stress in cancer cells. In those cells we found that DNAJB12 and DNAJB14 bind to HSC70 and they recruit SGTA upon stress. We also tested the binding between DNAJB12 and DNAJB14, in unstressed conditions, there was a basal binding between both, this interaction was stronger during ER stress. Those data are now added to Figure 5 and Figure S5 and the discussion was edited accordingly.

The binding of DNAJB12 to SGTA under stress conditions in Fig5B looks much more convincing than SGTA to DNAJB12 in Fig 5A. Bands in all blots need to be quantified from 3 independent experiments, and repeated if not already n=3. If this is solely a technical difference, please explain in the text.

The conclusions drawn from this interaction data are important and shold be elaborated upon to support th claims made in the paper. The authors may also chose to expand the pulldowns to demonstrate their claims made on olidomerisation of DNAJB12 and 14 here. It is also clear that the interaction data of the SGTA with ER-resident proteins AGR2, PRDX4 and DNAJB11 is strong. The authors may want to draw on this in their hypotheses of the mechanism. I would imagine a complex such as DNAJB14/DNAJB12 - SGTA - AGR2/PRDX4/DNAJB11 would be logical. Have any experiments been performed to prove if complexes like this would form?

Answer: In Figure 5A we used the Flp-In T-REx-293 cells as it is easier to control and to tune up and down the expression levels of DNAJB12 and DNAJB14. T-REx-293 are highly sensitive to ER stress, they do not die (as we did not observe apoptosis markers to be elevated) but they float and can regrow after the stress is gone. In Figure 5B we are using ER stress without the need to express DNAJB12 in A549 cell line. In order to further verify those data, we repeated the IP in another cell line as well to confirm the data in 5B. We also repeated the IP in 5A with anti-FLAG antibody to improve the IP and to specifically map he interaction with the overexpressed FLAG-DNAJB12 (discussed above). All experiments were done in triplicates and added to Figure 5 and Figure S5.

We agree with the reviewer on the complex between the refluxed proteins and SGTA. We believed that SGTA may form a complex with other refluxed ER-proteins but we were unable to see an interaction between AGR2-DNAJB11 in the cytosolic fraction or between AGR2-PRDX4 in the conditions tested in the cytosolic fraction. We could not do this in the whole cell lysate because those proteins bind each other in the ER. Finally, our structural prediction using Alpha-fold suggests that the interaction between SGTA and the refluxed AGR2 (and probably others) is redox depending and that it requires disulfide bridge between cysteine 81 on AGR2 and cysteine 153 on SGTA. Thus, we hypothesize that SGTA binds one refluxed protein at the time.

We repeated the figure with improvement: (1) using more cells in order to increase the amount of IP-ed proteins and to overcome the problem of the faint bands, (2) performing the IP with the FLAG antibodies instead of the DNAJB12 endogenous antibodies.

Fig 5B: It is clear that DNAJB12 interacts with SGTA. The authors state that DNAJB14 also interacts with SGTA under normal and stress conditions, but the band in 25/50 Tg is very feint. Why would there be stronger binding at the 2 extremes than during low stress induction? In the input, there is a much higher expression of DNAJB14 in 50 Tg. What does this say about the interaction? Is there an effect of ER stress on DNAJB14 expression? A negative control should be included to show any background binding, such as a "beads only" control

__Answer: __DNAJB14 does not change with ER stress as shown in the Ips (Input) and in the qPCR experiment in Figure S5I. We added beads only control, we also added new Ips to assess the binding between DNAJB14 and DNAJB12, and between DNAJB14-SGTA. All the new Ips and controls now added as Figure 5 and Figure S5.

Fig 5C data is sound, although a negative control should be included.

Answer: Negative control was added in Figure S5.

__Results section 4____ __

Fig 6A-B: Given that there is the complexity of overexpression v KD of DNAJB12 v 14 causing similar effects on p53 actvity (Fig 2 v 3), it would be interesting to see whether the effect of overexpression mirrors the results in Fig 6A. Is it known what SGTA overexpression does (optional)?

Answer: In the overexpression system, cells overexpressing DNAJB12 start to die between 24-48 hours as shown in Figure S3C. Thus, it is difficult to assay the proliferation of these cells in those conditions. On the other hand, overexpression of Myc-tagged SGTA in A549 cells, MCF7 or T-ReX293 did not show any reflux of ER-proteins to the cytosol and it didn’t show any significant changes in the proliferation index (Figure Reviewers only RV2).

Fig 6D: resolution very low

Answer: Figure 6D was changed

__ __ Fig 6C-D: There is an interesting difference though between the proposed cytosolic actions of the refluxed proteins. You show that AGR2, PRDX4 and DNAJB11 all bind to SGTA in stress conditions, but in the schematics you show: DNAJB11 binding to HSC70 through SGTA (not shown in the paper), then also PDIA1, PDIA3 binding to SGTA and AGR2 binding to SGTA. What role does SGTA have in these varied reactions? Sometimes it is depicted as an intermediate, sometimes a lone binder, what is its role as a binder? It should be clarified which interactions are demonstrated in the paper (or before) and which are hypothesized in a graphical way (eg. for hypotheses dotted outlines or no solid fill etc). The schematics also suggest that DNAJB14 binding to HSC70 and SGTA is inducible in stress conditions, as is PDIA3, which is not shown in the paper. Discussion "In cancer cells, DNAJB12 and DNAJB14 oligomerize and recruit cytosolic chaperones and cochaperones (HSC70 and SGTA) to reflux AGR2 and other ER-resident proteins and to inhibit wt-p53 and probably different proapoptotic signaling pathways (Figure 5, and Figure 6C-6D)." You havent shown oligomerisation between DNAJB12/14. Modify the text to make it clear that it is a hypothesis.

Answer: We removed “oligomerize” from the text and added that it as a hypothesis. Figure (C-D) also were changed to be compatible with the text.

Minor comments:

__ __ It would be useful to have page or line numbers to help with document navigation, please include them. Typos and inconsistency in how some proteins are named throughout the manuscript

Answer: Page numbers and line numbers are added. Typos are corrected

Title: Include reference to reflux. Suggest: "chaperone complexes (?proteins) reflux from the ER to cytosol..." I presume it would be more likely that the proteins go separately rather than in complex. Do you have any ideas on the size range of proteins that can undergo this process?

Answer: this is true, proteins may cross the ER membrane separately and then be in a complex with cytosolic chaperones. The title is changed accordingly. As discussed earlier, the protein we chose were of different sizes to show that they are refluxed independently of their size. Moreover, our previous work showed that the proteins that were refluxed are of different sizes. Most importantly UGGT1 (around 180 Kda) which is reported to deploy to the cytosol upon viral infection (Huang et al. 2017; Sicari et al. 2020). In this study we used AGR2 (around 19 Kda) and HYOU1 (150Kda).

ERCY in abstract, ERCYS in intro. There are typos throughout, could be a formatting problem, please check

Answer: Checked and corrected

What about the selection of refluxed proteins? Is this only a certain category of proteins? Could it be anything? Have you looked at other cargo / ER resident proteins?

__ ____Answer: __in our previous study by (Sicari, Pineau et al. 2020) we looked at many other proteins especially glycoproteins from the ER. In (Sicari, Pineau et al. 2020) we used mass spectrometry in order to identify new refluxed proteins and we found 26 new glycoprotein that are refluxed from cells treated with ER stressor and from human tissues obtained from GBM patients (Sicari, Pineau et al. 2020).

We previously showed that AGR2 is refluxed from the ER to the cytosol to bind and inhibit p53 (Sicari, Pineau et al. 2020). Here, we selected AGR2 because we know that (1) it is refluxed, and (2) we know which novel functions it acquires in the cytosol so we are able to measure and provide a physiological significance of those novel functions when the levels of DNAJB12 and DNAJB14 are altered. Moreover, we selected DNAJB11 (41 kDa) and HYOU1 (150 kDa) proteins to show that alteration in DNAJB12 or DNAJB14 prevent the reflux small, medium and large protein (independently of their size). We also showed earlier by mass spectrometry analysis that the refluxed proteins range from small to very large proteins such as UGGT1, thus we believe that soluble ER-proteins can be substrates of ERCYS independently of their size. In the discussion, we added a note that the reflux by the cytosolic and ER chaperones operates on different proteins independently of their size.

"Their role in ERCYS and cells' fate determination depends..." Suggest change to "Their role in ERCYS and determination of cell fate..."

Answer: changed and corrected

I think that the final sentence of the intro could be made stronger and more concise. There's a repeat of ER and cytosol. Instead could you comment on the reflux permitting new interactions between proteins otherwise spatially separated, then the effect on wt-p53 etc.

Answer: The sentence was rephrased as suggested to “ In this study, we found that HLJ1 is conserved through evolution and that mammalian cells have five putative functionality orthologs of the yeast HLJ1. Those five DNAJ- proteins (DNAJB12, DNAJB14, DNAJC14, DNAJC18, and DNAJC30) reside within the ER membrane with a J-domain facing the cytosol (Piette et al. 2021; Malinverni et al. 2023). Among those, we found that DNAJB12 and DNAJB14, which are strongly related to the yeast HLJ1 (Grove et al. 2011; Yamamoto et al. 2010), are essential and sufficient for determining cells' fate during ER stress by regulating ERCYS. Their role in ERCYS and determining cells' fate depends on their HPD motif in the J-domain. Downregulation of DNAJB12 and DNAJB14 increases cell toxicity and wt-p53 activity during etoposide treatment. Mechanistically, DNAJB12 and DNAJB14 interact and recruit cytosolic chaperones (HSC70/SGTA) to promote ERCYS. This later interaction is conserved in human tumors including colorectal cancer.

In summary, we propose a novel mechanism by which ER-soluble proteins are refluxed from the ER to the cytosol, permitting new inhibitory interactions between spatially separated proteins. This mechanism depends on cytosolic and ER chaperones and cochaperones, namely DNAJB12, DNAJB14, SGTA, and HSC70. As a result, the refluxed proteins gain new functions to inhibit the activity of wt-p53 in cancer cells. “

__Figure legends: __

In some cases the authors state the number of replicates, but this should be stated for all experiments. If experiments don't already include 3 independent repeats, this should be done. Check text for typos, correct letter capitalisation, spaces and random bold text (some of this could be from incompatability when saving as PDF)

Answer: all experiments were repeated at least three times. The number of repeats is now indicated in the figure legends of each experiment. Typos and capitalization is corrected as well.

Fig2E: scrambled not scramble siRNA

Answer: corrected

Fig 3: "to expel" is a term not used in the rest of the paper for reflux. Useful to remain consistent with terminology where possible

Answer: Rephrased and corrected

Results section 1:

"Protein alignment of the yeast HLJ1p showed high amino acids similarity to the mammalian..."

Answer: Rephrased to “ Comparing the amino acid sequences revealed significant similarity between the yeast protein HLJ1p and the mammalian proteins DNAJB12 and DNAJB14”

__ __ Fig 1C: state in legend which organism this is from (presumably human)

Answer: in Figure 1C legends it is stated that: “ the HPD motif within the J-domain is conserved in HLJ-1 and its putative human orthologs DNAJB12, DNAJB14, DNAJC14, DNAJC18, and DNAJC30.”

Results Section 2

"Test the two strongest hits DNAJB12/14" Add reference to previous paper showing this

Answer: the references were added.

__ __ "In the WT and J-protein-silenced A549 cells, there were no differences in the cytosolic enrichment of the three ER resident proteins AGR2, DNAJB11, and HYOU1 in normal and unstressed conditions (Figure 2A-C and Figure S2C)." I think that this is an oversimplification, and in your following discussion, you show this it's more subtle than this.

Answer: We expanded on this both in the discussion and the results section.

__ __ The text here isn't so clear: normal and unstressed conditions? Do you mean stressed? Please be careful in your phrases: "DNAJB12-silenced cells are slightly affected in AGR2 and DNAJB11 cytosolic accumulation but not HYOU1." This is the wrong way around. DNAJB12 silencing effects AGR2, not that AGR2 effects the cells (which is how you have written it). This also occurs agan in the next para:

Answer: Normal cells are non-cancer cells. Unstressed conditions= without ER stress. The sentence was rephrased to: In the absence of ER stress, the cytosolic levels of the three ER-resident proteins (AGR2, DNAJB11, and HYOU1) were similar in wild-type and J-protein-silenced A549 cells.

"During stress, DNAJB12/DNAJB14 double knockdown was highly affected in the cytosolic..." I think you mean it highly affected the cytosolic accumulation, not that it was affected by the cytosolic accumulation. Please change in the text

Answer: the sentence is now rephrased to” During stress, double knockdown of DNAJB12 and DNAJB14 highly affected the cytosolic accumulation of all three tested proteins”

__ __ "DNAJB12 and DNAJB14 are strong hits of the yeast HLJ1" Not clear, I presume you mean they are likely orthologues? Top candidates for being closest orthologues?

Answer: this is correct, the sentence is rephrased and corrected

__ __ Fig 2D: typos in WB labelling? I think Tm should be - - +, not - + +as it is now (if it's not a typo, you need more controls, eto alone.

Answer: the labeling is now corrected

Fig 2D-E-F typos for DKD? D12/D12 or D12/14?

Answer: This is correct, thank you for pointing this out. The labeling in corrected

__ __ "We assayed the phosphorylation state of wt- p53 and p21 protein expression levels (a downstream target of p53 signaling) during etoposide treatment." What are the results of this? Explain what Fig 2D-E shows, then build on this with the +Tm results. Results should be explained didactically to be clear.

Answer: The paragraph was edited and we explained the results: In these conditions, we saw an increase in the phosphorylation of wt-p53 in the control cells and in cells knocked-down with DNAJB12, DNAJB14 or both. This phosphorylation increased the protein levels of p21 as well (Figure 2D-G). Tm addition to cells treated with etoposide resulted in a reduction in wt-p53 phosphorylation, and as a consequence, the p21 protein levels were also decreased (Figure 2D-G and Figure S2O). Cells lacking DNAJB12 or DNAJB14 have partial protection in wt-p53 phosphorylation and p21 protein levels. Silencing both proteins in A549 and MCF7 cells rescued wt-p53 phosphorylation and p21 levels (Figure 2D-G and Figure S2D). Moreover, similar results were obtained when we assayed the transcriptional activity of wt-p53 in cells transfected with a luciferase reporter under the p53-DNA binding site (Figure 2H). These data confirm that DNAJB12 and DNAJB14 are involved in ER protein reflux and the inhibition of wt-p53 activity during ER stress.

"(Figure 2D- E). Cells lacking DNAJB12 and or DNAJB14 have partial protection in wt-p53 phosphorylation and p21 protein levels."

Answer: This sentence is now removed

You comment on p53 phosphorylation, but you haven't quantified this. This should be done, normalized to p53 levels, if you want to draw these conclusions, especially as total p53 varies between condition. Does Eto increase p53 txn? Does Tm alone increase p53 activity/phospho-p53? These are shown in the Sicari EMBO reports paper in 2021, you should briefly reference those.

Answer: The blots are now quantified and new blot is added to Figure S2D. The Paragraph was edited and referenced to our previous paper (Sicari et al. 2021). “We then wanted to examine whether the gain of function of AGR2 and the inhibition of wt-p53 depends on the activity of DNAJB12 and DNJAB14. We assayed the phosphorylation state of wt-p53 and p21 protein expression levels (a downstream target of wt-p53 signaling) during etoposide treatment. In these conditions, there was an increase in the phosphorylation of wt-p53 in the control cells and in cells knocked down with DNAJB12, DNAJB14, or both. This phosphorylation also increases protein levels of p21 (Figure 2D-G and Figure S2O). Tm addition to cells treated with etoposide resulted in a reduction in wt-p53 phosphorylation, and as a consequence, the p21 protein levels were also decreased (Figure 2D-G and Figure S2O). Silencing DNAJB12 and DNAJB14 in A549 and MCF-7 cells rescued wt-p53 phosphorylation and p21 levels (Figure 2D-G and Figure S2O). Moreover, similar results were obtained when we assayed the transcriptional activity of wt-p53 in cells transfected with a luciferase reporter under the p53-DNA binding site (Figure 2H). In the latter experiment, etoposide treatment increased the luciferase activity in all the cells tested. Adding ER stress to those cells decreased the luciferase activity except in cells silenced with DNAJB12 and DNAJB14.

These data confirm that DNAJB12 and DNAJB14 are involved in the reflux of ER proteins in general and AGR2 in particular. Inhibition of DNAJB12 and DNAJB14 prevented the inhibitory interaction between AGR2 and wt-p53 and thus rescued wt-p53 phosphorylation and its transcriptional activity as a consequence. “

Fig3A: overexpression of DNAJB12 decreases Eto induced p53 but not at steady state. Is this because at steady state the activity is already basal? Or is there another reason?

Answer: yes, at steady state the activity is already basal

Switch Figs S3D and S3C as they are not referred to in order. Also Fig S3C: vary colour (or add pattern) on bars more between conditions

Answer: The Figures now are called by their order in the new version. Colors are now added to Figure S3C.

Need to define HLJ1 at first mention

Answer: defined as” HLJ1 - High copy Lethal J-protein -an ER-resident tail-anchored HSP40 cochaperone.

Results section 3

HSC70 cochaperone (SGTA) defined twice

Answer: the second one was removed

"These data are important because SGTA and the ER-resident proteins (PRDX4, AGR2, and DNAJB11) are known to be expressed in different compartments, and the interaction occurs only when those ER-resident proteins localize to the cytosol." Is there a reference for this?

Answer: Peroxireoxin 4 is the only peroxerodin that is expressed in the ER. AGR2 and DNAJB11 are also ER luminal proteins that are known to be solely expressed in the ER. SGTA is part of the cytosolic quality control system and is expressed in the cytosol. The references are added in the main text.

Results section 4

"by almost two folds"

Answer: corrected

Fig 6A: It seems strange that the difference between purple and blue bars in scrambled, and D14-KD are very significant but D12-KD is only significant. Why is this? The error bars don't look that different. It would be interesting to see the individual means for each different replicate.

Answer: Thank you for pointing this, the two asterixis were aligned in the middle as one during figure alignments. In D14 the purple one has a lower error bar thus this changes the significance when compared to the blue while in D12-KD, the error bars in the eto treatment and the eto-Tm both are slightly higher. Graphs of the three different replicates are now added in Figure S6. Each one of the three biological replicates was repeated in three different technical repeats (averaged in the graphs).

Figures: Fig 6A: Scale bars not well placed. Annotation on final set should be D12/D14 DKD?

Answer: both were Corrected

__Discussion __47. The authors mention that they want to use DNAJB12/4-HSC70/SGTA axis to impair cancer cell fitness: What effect would this have though in a non cancer model? Would this be a viable approach Although it is obviously early days, which approach would the authors see as potentially favorable?

Answer: In our previous study we used an approach to target AGR2 in the cytosol because the reflux of AGR2 occurs only in cancer cells and not in normal cells. In that study we targeted AGR2 with scFv that targets AGR2 and is expressed in the cytosol, in this case it will target AGR2 in the cytosol which only occurs in cancer. Here, we suggest to target the interaction between the refluxed proteins and their new partners in the cytosol or to target the mechanism that causes their reflx to the cytosol by inhibiting for instance the interaction between SGTA and DNAJB proteins.

---

__ __ Second para: Should be "Here we present evidences"

Answer: we replaced with “Here we present evidences”

"DNAJB12 overexpression was also sufficient to promote ERCYS by refluxing AGR2 and inhibit wt-p53 signaling in cells treated with etoposide" Suggest:

Answer: DNAJB12 overexpression is also sufficient to promote ERCYS by refluxing AGR2 and inhibit wt-p53 signaling in cancer cells treated with etoposide (Figure 3). This suggests that it is enough to increase the levels of DNAJB12 without inducing the unfolded protein response in order to activate ERCYS. Moreover, the downregulation of DNAJB12 and DNAJB14 rescued the inhibition of wt-p53 during ER stress (Figure 2). Thus, wt-p53 inhibition is independent of the UPR activation but depends on the inhibitory interaction of AGR2 with wt-p53 in the cytosol.

.

DNAJB12 overexpression was also sufficient to promote ERCYS by increasing reflux of AGR2 and inhibition of wt-p53 signaling in cells treated with etoposide

Answer: This sentence is repeated twice and was removed

"Moreover, DNAJB12 was sufficient to promote this phenomenon and cause ER protein reflux by mass action without causing ER stress (Figure 3, Figure 4, and Figure S3)." You dont look at induction of ER stress here, please change the text or explain in more depth with refs if suitable

Answer: In the initial submission and in the revised version we assayed the activation of the UPR by looking at the levels of spliced Xbp1 and Bip in the different conditions when DNAJB12 and DNAJB14 are overexpressed (Figure S3C and S3D). Our data show that although DNAJB12 overexpression induces ERCYS, there was no UPR activation.

The mention of viruses is sparse in this paper. If it is a main theory, put it more centrally to the concept, and explain in more detail. As it is, its appearance in the final sentence is out of context.

Answer: DNAJB12 and DNAJB14 were reported to facilitate the escape of non-envelope viruses from the endoplasmic reticulum to the cytosol. The mechanism of non-envelope penetration is highly similar to the reflux of proteins from the ER to the cytosol. Interestingly, this mechanism takes place when the DNAJB12 and DNAJB14 form a complex with chaperones from both the ER and the cytosol including HSC70, SGTA and BiP (Walczak et al. 2014; Goodwin et al. 2011; Goodwin et al. 2014)..

Moreover, the UGGT1 that was independently found in our previous mass spectrometry analysis of the digitonin fraction obtained from HEK293T cells treated with the ER stressor thapsigargin and from isolated human GBM tumors (Sicari et al. 2020), is known to deploy to the cytosol upon viral infection (Huang et al. 2017; Sicari et al. 2020). We therefore hypothesized that the same machinary that is known to allow viruses to escape the ER to penetrate the cytosol may play an important role in the reflux of ER proteins to the cytosol.

Because ER protein reflux and the penetration of viruses from the ER to the cytosol behave similarly, we speculate that viruses hijacked an evolutionary conserved machinery -ER protein reflux- to penetrate to the cytosol. This is key because it was also reported that during the process of nonenveloped viruses penetration, large, intact and glycosylated viral particles are able to penetrate the ER membrane on their way to the cytosol (Inoue and Tsai 2011).

Action: we developed the discussion around this point and clarified it better because we believe it central to show that viruses hijacked this conserved mechanism.

**Referees cross-commenting**

I agree with the comments from Reviewer 1.

Reviewer 2 also is correct in many ways, but I think that they have somewhat overlooked the relevance of the ER-stress element and treatments. The authors do need to reference past papers more to give a full story, as this includes the groups own papers, I don't think that it is an ethical problem but rather an oversight in the writing. Regarding reviewer 2's concerns about overexpression levels and cell death, the authors do use an inducible cell line and show the levels of DNAJB12 induced (could CRISPR also be considered?). This could be used to further address reviewer 2's concerns. It would also be useful to see data on cell death in the conditions used in the paper. Re concerns about ER integrity, this could be addressed by using IF (or EM) to show a secondary ER marker that remains ER-localised, and this would also be of interest regarding my comment on which categories of proteins can undergo reflux. If everything is relocalised, then reviewer 2's point would be validated.

Reviewer #3 (Significance (Required)):

Significance

General assessment: This paper robustly shows that the yeast system of ER to cytosol reflux of ER-resident proteins is conserved in mammalian cells, and it describes clearly the link between ER stress, protein reflux and inhibition of p53 in mammalian cells. The authors have the tools to delve deeper into this mechanism and robustly explore this pathway, however the mechanistic elements - where not instantly clear from the results - have been over interpreted somewhat The results have been oversimplified in their explanations and some points and complexities of the study need to be addressed further to make the most of them - these are often some of the more interesting concepts of the paper, for example the differences in DNAJB12/14 and how the proteins orchestrate in the cytosol to play their cytosol-specific effects. I think that many points can be addressed in the text, by the authors being clear and concise with their reporting, while other experiments would turn this paper from an observational one, into a very interesting mechanistic one.

Advance: This paper is based on previous nice papers from the group. It is a nice progressions from yeast, to basic mechanism, to physiological model. But as mentioned, without a strong mechanistic improvement, the paper would remain observatory.

Audience: This paper is interesting to cell biologists (homeostasis, quality control and trafficking) as well as cancer cell biologists (fitness of cancer cells and homeostasis) and it is a very interesting demonstration of a process that is a double edged sword, depending on the environment of the cells.

My expertise: cell biology, trafficking, ER homeostasis

Answer: We would like to thank the reviewer for his/her positive feedback on our manuscript. All the comments of the three reviewers are now addressed and the manuscript has been strengthen. We put more emphasis on the mechanistic aspect with more Ips and knockdowns. We also added data to show that it is physiologically relevant. We hope that after that the revised version addressed all the concerns raised by the reviewers.

Goodwin, E. C., A. Lipovsky, T. Inoue, T. G. Magaldi, A. P. Edwards, K. E. Van Goor, A. W. Paton, J. C. Paton, W. J. Atwood, B. Tsai, and D. DiMaio. 2011. 'BiP and multiple DNAJ molecular chaperones in the endoplasmic reticulum are required for efficient simian virus 40 infection', MBio, 2: e00101-11.

Goodwin, E. C., N. Motamedi, A. Lipovsky, R. Fernandez-Busnadiego, and D. DiMaio. 2014. 'Expression of DNAJB12 or DNAJB14 causes coordinate invasion of the nucleus by membranes associated with a novel nuclear pore structure', PLoS One, 9: e94322.

Grove, D. E., C. Y. Fan, H. Y. Ren, and D. M. Cyr. 2011. 'The endoplasmic reticulum-associated Hsp40 DNAJB12 and Hsc70 cooperate to facilitate RMA1 E3-dependent degradation of nascent CFTRDeltaF508', Mol Biol Cell, 22: 301-14.

Huang, P. N., J. R. Jheng, J. J. Arnold, J. R. Wang, C. E. Cameron, and S. R. Shih. 2017. 'UGGT1 enhances enterovirus 71 pathogenicity by promoting viral RNA synthesis and viral replication', PLoS Pathog, 13: e1006375.

Igbaria, A., P. I. Merksamer, A. Trusina, F. Tilahun, J. R. Johnson, O. Brandman, N. J. Krogan, J. S. Weissman, and F. R. Papa. 2019. 'Chaperone-mediated reflux of secretory proteins to the cytosol during endoplasmic reticulum stress', Proc Natl Acad Sci U S A, 116: 11291-98.

Inoue, T., and B. Tsai. 2011. 'A large and intact viral particle penetrates the endoplasmic reticulum membrane to reach the cytosol', PLoS Pathog, 7: e1002037.

Malinverni, D., S. Zamuner, M. E. Rebeaud, A. Barducci, N. B. Nillegoda, and P. De Los Rios. 2023. 'Data-driven large-scale genomic analysis reveals an intricate phylogenetic and functional landscape in J-domain proteins', Proc Natl Acad Sci U S A, 120: e2218217120.

Piette, B. L., N. Alerasool, Z. Y. Lin, J. Lacoste, M. H. Y. Lam, W. W. Qian, S. Tran, B. Larsen, E. Campos, J. Peng, A. C. Gingras, and M. Taipale. 2021. 'Comprehensive interactome profiling of the human Hsp70 network highlights functional differentiation of J domains', Mol Cell, 81: 2549-65 e8.

Sicari, D., F. G. Centonze, R. Pineau, P. J. Le Reste, L. Negroni, S. Chat, M. A. Mohtar, D. Thomas, R. Gillet, T. Hupp, E. Chevet, and A. Igbaria. 2021. 'Reflux of Endoplasmic Reticulum proteins to the cytosol inactivates tumor suppressors', EMBO Rep: e51412.

Sicari, Daria, Raphael Pineau, Pierre-Jean Le Reste, Luc Negroni, Sophie Chat, Aiman Mohtar, Daniel Thomas, Reynald Gillet, Ted Hupp, Eric Chevet, and Aeid Igbaria. 2020. 'Reflux of Endoplasmic Reticulum proteins to the cytosol yields inactivation of tumor suppressors', bioRxiv.

Walczak, C. P., M. S. Ravindran, T. Inoue, and B. Tsai. 2014. 'A cytosolic chaperone complexes with dynamic membrane J-proteins and mobilizes a nonenveloped virus out of the endoplasmic reticulum', PLoS Pathog, 10: e1004007.

Yamamoto, Y. H., T. Kimura, S. Momohara, M. Takeuchi, T. Tani, Y. Kimata, H. Kadokura, and K. Kohno. 2010. 'A novel ER J-protein DNAJB12 accelerates ER-associated degradation of membrane proteins including CFTR', Cell Struct Funct, 35: 107-16.

Youker, R. T., P. Walsh, T. Beilharz, T. Lithgow, and J. L. Brodsky. 2004. 'Distinct roles for the Hsp40 and Hsp90 molecular chaperones during cystic fibrosis transmembrane conductance regulator degradation in yeast', Mol Biol Cell, 15: 4787-97.

Reviewer #2 (Public Review):

Summary:

Franke et al. characterize the representation of color in the primary visual cortex of mice, highlighting how this changes across the visual field. Using calcium imaging in awake, head-fixed mice, they characterize the properties of V1 neurons (layer 2/3) using a large center-surround stimulation where green and ultra-violet colors were presented in random combinations. Clustering of responses revealed a set of functional cell-types based on their preference to different combinations of green and UV in their center and surround. These functional types were demonstrated to have different spatial distributions across V1, including one neuronal type (Green-ON/UV-OFF) that was much more prominent in the posterior V1 (i.e. upper visual field). Modelling work suggests that these neurons likely support the detection of predator-like objects in the sky.

Strengths:

The large-scale single-cell resolution imaging used in this work allows the authors to map the responses of individual neurons across large regions of the visual cortex. Combining this large dataset with clustering analysis enabled the authors to group V1 neurons into distinct functional cell types and demonstrate their relative distribution in the upper and lower visual fields. Modelling work demonstrated the different capacity of each functional type to detect objects in the sky, providing insight into the ethological relevance of color opponent neurons in V1.

Weaknesses:

It is unfortunate the authors were unable to provide stronger mechanistic insights into how color opponent neurons in V1 are formed.

Overall, this study will be a valuable resource for researchers studying color vision, cortical processing, and the processing of ethologically relevant information. It provides a useful basis for future work on the origin of color opponency in V1 and its ethological relevance.

A obvious sign he likes it, and it was not through verbal fuddling that he communicated this, but through his body's involuntary reaction that he cannot plan nor control.

This work has been peer reviewed in GigaScience (see paper), which carries out open, named peer-review. These reviews are published under a CC-BY 4.0 license and were as follows:

Reviewer name: Virgilio Gail Ponferrada (Original submission)

The manuscript is well written and easy to understand. It will be a good contribution to the Xenopus research community as well as a useful reference for the field of developmental and amphibian biology.

I suggest the following revisions: - For the graphical abstract try alternating NF stage numbers above and below samples for a cleaner look, adult male and adult female can both remain at the top. - Appreciate the rationale for providing the microCT analysis presented in this manuscript and choices of late stage tadpoles, pre- and prometamorphosis, through metamporphosis to the adult male and female frog. - For the head development section authors can make reference to the Xenhead drawings, Zahn et al. Development 2017. - Head Development section paragraph 4, change word from "gender" to "sex." - Supplementary Table 3. Change "gender-related" to "sex-related." - Micro-CT Data Analysis of Long Bone Growth Dynamics section paragraph 1 change "in terms of gender" to "in terms of sex." - Figure 4 panels A and B don't reflect the observation that adult females are enlarged males. While the authors state that the view of the male and female skeletons are maximized and not proportional as stated in the caption, suggest that scale bars be employed and the images adjusted to show the size relationship difference between the sexes as in Figure 1. On first glance and perhaps to those not as familiar with the difference in sex size in Xenopus that in this particular example of the adult male image being more spread out compared to the image of the female, it feels misleading. - Ossification Analysis section paragraph 2 change "frog's gender" to "frog's sex." - Figure 5 panel A, the label is overlapping "NF 59." For panels B and B' scale bars on these panels would help the reader understand the proportions. Yes, there is the 3mm scale bar from panel A and as stated in the caption, but including them in the B panels could help even if panel B had a scale bar labeled at 0.25 mm and panel B' was 3 mm. - Segmentation of Selected Internal Soft Organ section, perhaps more commentary on the ability to observe the development of the segmentation of the brain regions: cbh: cerebral hemispheres; cbl: cerebellum; dch: diencephalon; mob: medulla oblongata; opl: optic lobes; sp: spinal cord while clearly shown in Figure 6, some accompanying description in the text would help readers in general or give the implication that microCT analysis of mutant or diseased frogs could help identify physical characteristics of frogs with developmental or neurological disorders. This would help transition from the analysis of a specific organ to the next section Further Biological Potential of Xenopus's Data. - These analyses, while thorough accompanied by novel visuals, require statistical implementation of multiple tadpoles and frogs per NF stage to account for variation in samples and to bolster the claims stated in skull thickness, the head mass and eye distance changes, increased length of the long bones during maturation, and femural ossification cartilage to bone ratios. This may constitute a suggested major revision to perform these analyses.

The cost of this example outweighs the benifit or the utility.

eLife assessment

This paper describes an important advance in an in vitro neural culture system to generate mature, functional, diverse, and geometrically consistent cultures, in a 384-well format with defined dimensions and the absence of the necrotic core, which persists for up to 300 days. The well-based format and conserved geometry make it a promising tool for arrayed screening studies. Some of the evidence is incomplete and could benefit from a more direct head-to-head comparison with more standard culture methods and standardization of cell seeding density as well as further data on reproducibility in each well and for each cell line.

Reviewer #2 (Public Review):

Summary:

In this manuscript, van der Kroeg et al have developed a method for creating 3D cortical organoids using iPSC-derived neural progenitor cells in 384-well plates, thus scaling down the neural organoids to adherent culture and a smaller format that is amenable to high throughput cultivation. These adherent cortical organoids, measuring 3 x 3 x 0.2 mm, self-organize over eight weeks and include multiple neuronal subtypes, astrocytes, and oligodendrocyte lineage cells.

Strengths:

(1) The organoids can be cultured for up to 10 months, exhibiting mature dendritic spines, axonal myelination, and robust neuronal activity.

(2) Unlike free-floating organoids, these do not develop necrotic cores, making them ideal for high-throughput drug discovery, neurotoxicological screening, and brain disorder studies.

(3) The method addresses the technical challenge of achieving higher-order neural complexity with reduced heterogeneity and the issue of necrosis in larger organoids. The method presents a technical advance in organoid culture.

(4) The method has been demonstrated with multiple cell lines which is a strength.

(5) The manuscript provides high-quality immunostaining for multiple markers.

Weaknesses:

(1) Direct head-to-head comparison with standard organoid culture seems to be missing and may be valuable for benchmarking, ie what can be done with the new method that cannot be done with standard culture and vice versa, ie what are the aspects in which new method could be inferior to the standard.

(2) It would be important to further benchmark the throughput, ie what is the success rate in filling and successfully growing the organoids in the entire 384 well plate?

(3) For each NPC line an optimal seeding density was estimated based on the proliferation rate of that NPC line and via visual observation after 6 weeks of culture. It would be important to delineate this protocol in more robust terms, in order to enable reproducibility with different cell lines and amongst the labs.

Author response:

Public Reviews:

Reviewer #1 (Public Review):

Summary: 

Kroeg et al. describe a novel method for 2D culture human induced pluripotent stem cells (hiPSCs) to form cortical tissue in a multiwell format. The method claims to offer a significant advancement over existing developmental models. Their approach allows them to generate cultures with precise, reproducible dimensions and structure with a single rosette; consistent geometry; incorporating multiple neuronal and glial cell types (cellular diversity); avoiding the necrotic core (often seen in free-floating models due to limited nutrient and oxygen diffusion). The researchers demonstrate the method's capacity for long-term culture, exceeding ten months, and show the formation of mature dendritic spines and considerable neuronal activity. The method aims to tackle multiple key problems of in vitro neural cultures: reproducibility, diversity, topological consistency, and electrophysiological activity. The authors suggest their potential in high-throughput screening and neurotoxicological studies.

Strengths: 

The main advances in the paper seem to be: The culture developed by the authors appears to have optimal conditions for neural differentiation, lineage diversification, and long-term culture beyond 300 days. These seem to me as a major strength of the paper and an important contribution to the field. The authors present solid evidence about the high cell type diversity present in their cultures. It is a major point and therefore it could be better compared to the state of the art. I commend the authors for using three different IPS lines, this is a very important part of their proof. The staining and imaging quality of the manuscript is of excellent quality.

We thank the reviewer for the positive comments on the potential of our novel platform to address key problems of in vitro neural culture, highlighting the longevity and reproducibility of the method across multiple cell lines.

Weaknesses: 

(1) The title is misleading: The presented cultures appear not to be organoids, but 2D neural cultures, with an insufficiently described intermediate EB stage. For nomenclature, see: doi: 10.1038/s41586-022-05219-6. Should the tissue develop considerable 3D depth, it would suffer from the same limited nutrient supply as 3D models - as the authors point out in their introduction. 

We appreciate the opportunity to clarify this point. We respectfully disagree that the cultures do not meet the consensus definition of an organoid. In fact, a direct quote from the seminal nomenclature paper referenced by the reviewer states: “We define organoids as in vitro-generated cellular systems that emerge by self-organization, include multiple cell types, and exhibit some cytoarchitectural and functional features reminiscent of an organ or organ region. Organoids can be generated as 3D cultures or by a combination of 3D and 2D approaches (also known as 2.5D) that can develop and mature over long periods of time (months to years).” (Pasca et al, 2022 doi10.1038/s41586-022-05219-6). Therefore, while many organoid types indeed have a more spherical or globular 3D shape, the term organoid also applies to semi-3D or non-globular adherent organoids, such as renal (Czerniecki et al 2018, doi.org/10.1016/j.stem.2018.04.022) and gastrointestinal organoids (Kakni et al 2022, doi.org/10.1016/j.tibtech.2022.01.006). Accordingly, the adherent cortical organoids described in the manuscript exhibit self-organization to single radial structures consisting of multiple cell layers in the z-axis, reaching ~200um thickness (therefore remaining within the limits for sufficient nutrient supply), with consistent cytoarchitectural topology and electrophysiological activity, and therefore meet the consensus definition of an organoid.

(2) The method therefore should be compared to state-of-the-art (well-based or not) 2D cultures, which seems to be somewhat overlooked in the paper, therefore making it hard to assess what the advance is that is presented by this work. 

It was not our intention to benchmark this model quantitatively against other culture systems. Rather, we have attempted to characterize the opportunities and limitations of this approach, with a qualitative contrast to other culture methods. Compared to state-of-the-art 2D neural network cultures, adherent cortical organoids provide distinct advantages in:

(1) Higher order self-organized structure formation, including segregation of deeper and upper cortical layers.

(2) Longevity: adherent cortical organoids can be successfully kept in culture up to 1 year where 2D cultures typically deteriorate after 8-12 weeks.

(3) Maturity, including the formation of dendritic mushroom spines and robust electrophysiological activity.

(4) Cell type diversity including a more physiological ratio of inhibitory and excitatory neurons (10% GAD67+/NeuN+ neurons in adherent cortical organoids, vs 1% in 2D neural networks) and the emergence of oligodendrocyte lineage cells.

On the other hand, limitations of adherent cortical organoids compared to 2D neural network cultures are:

(1) Culture times for organoids are much longer than for 2D cultures and the method can therefore be more laborious and more expensive.

(2) Whole cell patch clamping is not easily feasible in the organoids because of the restricting dimensions of the 384well plates.

(3) Reproducibility is prominently claimed throughout the manuscript. However, it is challenging to assess this claim based on the data presented, which mostly contain single frames of unquantified, high-resolution images. There are almost no systematic quantifications presented. The ones present (Figure S1D, Figure 4) show very large variability. However, the authors show sets of images across wells (Figure S1B, Figure S3) which hint that in some important aspects, the culture seems reproducible and robust. 

We made considerable efforts to establish quantitative metrics to assess reproducibility. We applied a quantitative scoring system of single radial structures at different time points for multiple batches of all three lines as indicated in Figure S1D. This figure represents a comprehensive dataset in which each dot represents the average of a different batch of organoids containing 10-40 organoids per batch. To emphasize this, we will adapt the graph to better reflect the breadth of the dataset. Additional quantifications are given in Figure S2 for progenitor and layer markers for Line 1 and in Figure S5 for interneurons across all three lines, showing relatively low variability. That being said, we acknowledge the reviewer’s concerns and will modify the text to reduce the emphasis of this point, pending more extensive data addressing reproducibility across a wide range of parameters.

(4) What is in the middle? All images show markers in cells present around the center. The center however seems to be a dense lump of cells based on DAPI staining. What is the identity of these cells? Do these cells persist throughout the protocol? Do they divide? Until when? Addressing this prominent cell population is currently lacking. 

A more comprehensive characterization of the cells in the center remains a significant challenge due to the high cell density hindering antibody penetration. However, dye-based staining methods such as DAPI and the LIVE/DEAD panel confirm a predominance of intact nuclei with very minimal cell death. The limited available data suggest that a substantial proportion of the cells in the center are proliferative neural progenitors, indicated by immunolabeling for SOX2 and Ki67. We will add additional figures to support these findings. Furthermore, we are currently optimizing the conditions to perform single cell / nuclear RNA sequencing to further characterize the cellular composition of the organoids.

(5) This manuscript proposes a new method of 2D neural culture. However, the description and representation of the method are currently insufficient. <br /> (a) The results section would benefit from a clear and concise, but step-by-step overview of the protocol. The current description refers to an earlier paper and appears to skip over some key steps. This section would benefit from being completely rewritten. This is not a replacement for a clear methods section, but a section that allows readers to clearly interpret results presented later.

We will revise the manuscript to include a more detailed step-by-step overview of the protocol.

(b) Along the same lines, the graphical abstract should be much more detailed. It should contain the time frames and the media used at the different stages of the protocol, seeding numbers, etc. 

As suggested, we will also adapt the graphical abstract to include more detail.

Reviewer #2 (Public Review): 

Summary: 

In this manuscript, van der Kroeg et al have developed a method for creating 3D cortical organoids using iPSC-derived neural progenitor cells in 384-well plates, thus scaling down the neural organoids to adherent culture and a smaller format that is amenable to high throughput cultivation. These adherent cortical organoids, measuring 3 x 3 x 0.2 mm, self-organize over eight weeks and include multiple neuronal subtypes, astrocytes, and oligodendrocyte lineage cells.

Strengths: 

(1) The organoids can be cultured for up to 10 months, exhibiting mature dendritic spines, axonal myelination, and robust neuronal activity. 

(2) Unlike free-floating organoids, these do not develop necrotic cores, making them ideal for high-throughput drug discovery, neurotoxicological screening, and brain disorder studies.

(3) The method addresses the technical challenge of achieving higher-order neural complexity with reduced heterogeneity and the issue of necrosis in larger organoids. The method presents a technical advance in organoid culture.

(4) The method has been demonstrated with multiple cell lines which is a strength. 

(5) The manuscript provides high-quality immunostaining for multiple markers. 

We appreciate the reviewer’s acknowledgement of the strengths of this novel platform as a technical advance in organoid culture that reduces heterogeneity and shows potential for higher throughput experiments.

Weaknesses: 

(1) Direct head-to-head comparison with standard organoid culture seems to be missing and may be valuable for benchmarking, ie what can be done with the new method that cannot be done with standard culture and vice versa, ie what are the aspects in which new method could be inferior to the standard.

In our opinion, it would be extremely difficult to directly compare methods because of substantial differences. Most notably, whole brain organoids grow to large and irregular globular shapes, while adherent cortical organoids have a highly standardized shape confined by the limits of a 384-well. Moreover, it was not our intention to benchmark this model quantitatively against other culture systems. Rather, we have attempted to characterize the opportunities and limitations of this approach, with a qualitative contrast to other culture methods.

(2) It would be important to further benchmark the throughput, ie what is the success rate in filling and successfully growing the organoids in the entire 384 well plate? 

Figure S1D shows the success rate of organoid formation and stability of the organoid structures over time. In addition, we will add the number of wells that were filled per plate.

(3) For each NPC line an optimal seeding density was estimated based on the proliferation rate of that NPC line and via visual observation after 6 weeks of culture. It would be important to delineate this protocol in more robust terms, in order to enable reproducibility with different cell lines and amongst the labs. 

Figure S1C provides the relationship between proliferation rate and seeding density, allowing estimation of seeding densities based on the proliferation rate of the NPCs. However, we appreciate the reviewers feedback and will modify the methods to provide more detail.

Reviewer #3 (Public Review): 

Summary: 

Kroeg et al. have introduced a novel method to produce 3D cortical layer formation in hiPSC-derived models, revealing a remarkably consistent topography within compact dimensions. This technique involves seeding frontal cortex-patterned iPSC-derived neural progenitor cells in 384-well plates, triggering the spontaneous assembly of adherent cortical organoids consisting of various neuronal subtypes, astrocytes, and oligodendrocyte lineage cells. 

Strengths: 

Compared to existing brain organoid models, these adherent cortical organoids demonstrate enhanced reproducibility and cell viability during prolonged culture, thereby providing versatile opportunities for high-throughput drug discovery, neurotoxicological screening, and the investigation of brain disorder pathophysiology. This is an important and timely issue that needs to be addressed to improve the current brain organoid systems. 

We thank the reviewer for highlighting the strengths of our novel platform. We appreciate that all three reviewers agree that the adherent cortical organoids presented in this manuscript reliably demonstrate increased reproducibility and longevity. They also commend its potential for higher throughput drug discovery and neurotoxicological/phenotype screening purposes.

Weaknesses: 

While the authors have provided significant data supporting this claim, several aspects necessitate further characterization and clarification. Mainly, highlighting the consistency of differentiation across different cell lines and standardizing functional outputs are crucial elements to emphasize the future broad potential of this new organoid system for large-scale pharmacological screening.

We appreciate the feedback and will add more detail on consistency and standardization of functional outputs.

Author response:

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

eLife assessment:

Franke et al. explore and characterize the color response properties in the mouse primary visual cortex, revealing specific color opponent encoding strategies across the visual field. The data is solid; however, the evidence supporting some conclusions is incomplete. In its current form, the paper makes a useful contribution to how color is coded in mouse V1. Significance would be enhanced with some additional analyses and a clearer discussion of the limitations of the data presented.

We thank the reviewers for appreciating our manuscript. We have rewritten the conclusions of the paper to be more conservative and now more explicitly focus on color processing in mouse V1, rather than comparing V1 to the retina. Additionally, we discuss the limitations of our approach in detail in the Discussion section. Finally, we have addressed all comments from the reviewers below.

Referee 1 (Remarks to the Author):

In this study, Franke et al. explore and characterize color response properties across primary visual cortex, revealing specific color opponent encoding strategies across the visual field. The authors use awake 2P imaging to define the spectral response properties of visual interneurons in layer 2/3. They find that opponent responses are more pronounced at photopic light levels, and that diversity in color opponent responses exists across the visual field, with green ON/ UV OFF responses more strongly represented in the upper visual field. This is argued to be relevant for the detection of certain features that are more salient when using chromatic space, possibly due to noise reduction. In the revised version, Franke et al. have addressed the potential pitfalls in the discussion, which is an important point for the non-expert reader. Thus, this study provides a solid characterization of the color properties of V1 and is a valuable addition to visual neuroscience research.

My remaining concerns are based more on the interpretation. I’m still not convinced by the statement "This type of color-opponency in the receptive field center of V1 neurons was not present in the receptive field center of retinal ganglion cells and, therefore, is likely computed by integrating center and surround information downstream of the retina." and I would suggest rewording it in the abstract.

As discussed previously and now nicely added to the discussion, it is difficult to make a direct comparison given the different stimulus types used to characterize the retina and V1 recordings and the different levels of adaptation in both tissues. I will leave this point to the discussion, which allows for a more nuanced description of the phenomenon. Why do I think this is important? In the introduction, the authors argue that "the discrepancy [of previous studies] may be due to differences in stimulus design or light levels." However, while different light levels can be tested in V1, this cannot be done properly in the retina with 2P experiments. To address this, one would have to examine color-opponency in RGC terminals in vivo, which is beyond the scope of this study. Addressing these latter points directly in the discussion would, in my opinion, only strengthen the study.

We thank the reviewer for the feedback. We removed the sentence mentioned by the reviewer from the abstract, as well as from the summary of our results in the Introduction. Additionally, we now phrase the interpretation of the retinal results more conservatively and specifically highlight in the Discussion that comparing ex-vivo retinal to in-vivo cortical data is challenging. With these changes, we believe that the focus of the paper is explicitly defined to be on the neuronal representation of color in mouse visual cortex, rather than on the comparison of retinal and cortical color processing.

Minor:

In the abstract, the second sentence says that we already know the mechanisms in primates.

Unfortunately, I do not think this is true. First, primates refers to an order with several species, which might have adaptations to their color-processing. Second, I’m aware of several characterizations in "primates" that have led to convincing models (as referenced), but in my opinion, this is far from a true understanding the mechanisms, especially since very little is known about foveal color processing due to the difficulties of these experiments. Similarly in the introduction. "Primates" is indirectly defined as a species. Perhaps some rewording is needed here as well, since we know how different cone distributions can be in rodents (see Peichl’s work).

Thanks. We have reworded the Abstract and Introduction towards indicating that many studies have been performed in primate species, without suggesting that the mechanisms are described.

The legend in Fig. 2 has a "Fig. ???"

Fixed.

Referee 2 (Remarks to the Author):

Franke et al. characterize the representation of color in the primary visual cortex of mice, highlighting how this changes across the visual field. Using calcium imaging in awake, head-fixed mice, they characterize the properties of V1 neurons (layer 2/3) using a large center-surround stimulation where green and ultra-violet colors were presented in random combinations. Clustering of responses revealed a set of functional cell-types based on their preference to different combinations of green and UV in their center and surround. These functional types were demonstrated to have different spatial distributions across V1, including one neuronal type (Green-ON/UV-OFF) that was much more prominent in the posterior V1 (i.e. upper visual field). Modelling work suggests that these neurons likely support the detection of predator-like objects in the sky.

Strengths: The large-scale single-cell resolution imaging used in this work allows the authors to map the responses of individual neurons across large regions of the visual cortex. Combining this large dataset with clustering analysis enabled the authors to group V1 neurons into distinct functional cell types and demonstrate their relative distribution in the upper and lower visual fields. Modelling work demonstrated the different capacity of each functional type to detect objects in the sky, providing insight into the ethological relevance of color opponent neurons in V1.

We thank the reviewer for appreciating our study.

Weaknesses: While the study presents convincing evidence about the asymmetric distribution of color-opponent neurons in V1, the paper would greatly benefit from a more in-depth discussion of the caveats related to the conclusions drawn about their origin. This is particularly relevant regarding the conclusion drawn about the contribution of color opponent neurons in the retina. The mismatch between retinal color opponency and V1 color opponency could imply that this feature is not solely inherited from the retina, however, there are other plausible explanations that are not discussed here. Direct evidence for this statement remains weak.

Thanks for this comment. We removed the retinal findings from the abstract, as well as from the summary of our results in the Introduction. In addition, we now phrase the interpretation of the retinal results more conservatively and specifically highlight in the Discussion that comparing ex-vivo retinal to in-vivo cortical data is challenging. With these changes, we believe that the focus of the paper is explicitly defined to be on the neuronal representation of color in mouse visual cortex, rather than on the comparison of retinal and cortical color processing.

In addition, the paper would benefit from adding explicit neuron counts or percentages to the quadrants of each of the density plots in Figures 2-5. The variance explained by the principal components does not capture the percentage of color opponent cells. Additionally, there appear to be some remaining errors in the figure legend and labels that have not been addressed (e.g. ’??’ in Fig 2 legend).

Thank you for this suggestion. We believe that adding the numbers or percentages to the figure panels would make them too crowded. Instead, we have now mentioned in the Results section and the legends that the percentages of variance explained by the color (off-diagonal) and luminance axis (diagonal) correlate with the number of neurons located in the color (top left and bottom right) and luminance contrast quadrants (top right and bottom left), respectively. Together with the number of neurons in each plot stated in the legends and the scale bar indicating the number of neurons per gray level, we hope this approach provides clarity for the reader to interpret the panels. Additionally, we have fixed the broken reference in the legend of Fig. 2.

Overall, this study will be a valuable resource for researchers studying color vision, cortical processing, and the processing of ethologically relevant information. It provides a useful basis for future work on the origin of color opponency in V1 and its ethological relevance.

General Suggestions:

-  Please add possible caveats of using ETA method to the discussion section. For example, it is unclear to what extent ON/OFF cells are being overlooked by using ETA method.

We now discuss the limitations of the ETA approach in the Discussion section.

- The caveats of using the percentage of variance explained in the retina as evidence against V1 solely inheriting color-opponency from retinal output neurons are not adequately addressed. For example, could the mismatch in explained variance of the color axis between V1 and RGCs be explained by a subset of non-color opponent RGCs projecting elsewhere (not dLGN-V1) or that color opponent cells project to a larger number of neurons in V1 than non-color opponent cells? We suggest adding a paragraph to the discussion to address this issue.

We have removed these conclusions from the paper, more carefully interpret the retinal results and mention that comparing ex-vivo retina data with in-vivo cortical data is challenging.

- Please clarify how the different response types shown in Figure 5e-f lead to differences in noise detection and thereby differences in predator discriminability. For example, why does Gon/UVoff not respond to the noise scene while Goff/UVoff does?

We added this to the Results section.

- Please clarify the relationship between ETA amplitude, neural response probability, and neural response amplitude. For example, do color-opponent cells have equal absolute neural response amplitudes to the different colors?

Thank you for bringing up this point. The ETA is obtained by summing the stimulus sequences that elicit an event (i.e., response), weighted by the amplitude of the response. Consequently, the absolute amplitude of the ETA correlates with the calcium amplitude. Importantly, the ETA amplitudes of different stimulus conditions are comparable because they were estimated on the same normalized calcium trace. Therefore, comparing the absolute amplitudes of ETAs of color-opponent neurons reveals the response magnitude of the cells to different colors. We have now included this information in the Results section.

Abstract: - "more than a third of neurons in mouse V1 are color-opponent in their receptive field center". It is unclear what data supports this statement. Can you please provide a statement in the manuscript that supports this directly using the number of neurons?

We added the following sentence to the Results section: Nevertheless, a substantial fraction of neurons (33.1%) preferred color-opponent stimuli and scattered along the off-diagonal in the upper left and lower right quadrants, especially for the RF center.

Figure 2: - There is a ?? in the figure legend. Which figure should this refer to? - please provide explicit neuron counts/percentages for each quadrant in b.

We fixed the figure reference. We believe that adding the numbers or percentages to the figure panels would make them too crowded. Instead, we have now mentioned in the Results section and the legends that the percentages of variance explained by the color (off-diagonal) and luminance axis (diagonal) correlate with the number of neurons located in the color (top left and bottom right) and luminance contrast quadrants (top right and bottom left), respectively. Together with the number of neurons in each plot stated in the legends and the scale bar indicating the number of neurons per gray level, we hope this approach provides clarity for the reader to interpret the panels.

Figure 3: - Fig 3: Color scheme makes it very difficult to differentiate the different conditions, especially when printed.

Thanks we changed the color scheme.

- Add explicit neuron counts/percentages for each quadrant in b.

See above.

Figure 4: - Add explicit neuron counts/percentages for each quadrant in b.

See above.

Figure 5: - Add explicit neuron counts/percentages for each quadrant in c.

See above.

Methods: - "we modeled each response type to have a square RF with 10 degrees visual angle in diameter". There appears to be a mismatch between this statement and Figure 5e where 18 degrees is reported.

Thanks we fixed that.

Referee 3 (Remarks to the Author):

This paper studies chromatic coding in mouse primary visual cortex. Calcium responses of a large collection of cells are measured in response to a simple spot stimulus. These responses are used to estimate chromatic tuning properties - specifically sensitivity to UV and green stimuli presented in a large central spot or a larger still surrounding region. Cells are divided based on their responses to these stimuli into luminance or chromatic sensitive groups. The results are interesting and many aspects of the experiments and conclusions are well done; several technical concerns, however, limit the support for several main conclusions,

Limitations of stimulus choice The paper relies on responses to a large (37.5 degree diameter) modulated spot and surround region. This spot is considerably larger than the receptive fields of both V1 cells and retinal ganglion cells (it is twice the area of the average V1 receptive field). As a result, the spot itself is very likely to strongly activate both center and surround mechanisms, and responses of cells are likely to depend on where the receptive fields are located within the spot

(and, e.g., how much of the true neural surround samples the center spot vs the surround region). Most importantly, the surrounds of most of the recorded cells will be strongly activated by the central spot. This brings into question statements in the paper about selective activation of center and surround (e.g. page 2, right column). This in turn raises questions about several subsequent analyses that rely on selective center and surround activation.

Thank you for this comment. A similar point was raised by a reviewer in the first round of revision. We agree with the reviewers that it is critical to discuss both the rationale behind our stimulus design and its limitations to facilitate better interpretation by the reader.

To be able to record from many V1 neurons simultaneously, we used a stimulus size of 37.5 degree visual angle in diameter, which is slightly larger than center RFs of single V1 neurons (between 20 - 30 degrees visual angle depending on the stimulus, see here). The disadvantage of this approach is that the stimulus is only roughly centered on the neurons’ center RFs. To reduce the impact of potential stimulus misalignment on our results, we used the following steps: { For each recording, we positioned the monitor such that the mean RF across all neurons lies within the center of the stimulus field of view.

We confirmed that this procedure results in good stimulus alignment for the large majority of recorded neurons within individual recording fields by using a sparse noise stimulus (Suppl. Fig. 1a-c). Specifically, we found that for 83% of tested neurons, more than two thirds of their center RF, determined by the sparse noise stimulus, overlapped with the center spot of the color noise stimulus.

For analysis, we excluded neurons without a significant center STA, which may be caused by misalignment of the stimulus.

Together, we believe these points strongly suggest that the center spot and the surround annulus of the noise stimulus predominantly drive center (i.e. classical RF) and surround (i.e. extraclassical RF), respectively, of the recorded V1 neurons. This is further supported by the fact that color response types identified using an automated clustering method were robust across mice (Suppl. Fig. 6c), indicating consistent stimulus centering.

Nevertheless, we cannot exclude the possibility that the stimulus was misaligned for a subset of the recorded neurons used in our analysis. We agree with the reviewer that such misalignment might have caused the center stimulus to partially activate the surround. To further address this issue beyond the controls we have already implemented, one could compare the results of our approach with an approach that centers the stimulus on individual neurons. However, we believe that performing these additional experiments is beyond the scope of the current study.

To acknowledge the experimental limitations of our study and the concerns brought up by the reviewer, we have added the steps we perform to reduce the effects of stimulus misalignment in the Results section and discuss the problem of stimulus alignment in the Discussion in a separate section. With this, we believe our manuscript explains both the rationale behind our stimulus design as well as important limitations of the approach.

Comparison with retina A key conclusion of the paper is that the chromatic tuning in V1 is not inherited from retinal ganglion cells. This conclusion comes from comparing chromatic tuning in a previously-collected data set from retina with the present results. But the retina recordings were made using a considerably smaller spot, and hence it is not clear that the comparison made in the paper is accurate. For example, the stimulus used for the V1 experiments almost certainly strongly stimulates both center and surround of retinal ganglion cells. The text focuses on color opponency in the receptive field centers of retinal ganglion cells, but center-surround opponency seems at least as relevant for such large spots. This issue needs to be described more clearly and earlier in the paper.

Thanks for this comment. We removed the retinal findings from the abstract, as well as from the summary of our results in the Introduction. In addition, we now phrase the interpretation of the retinal results more conservatively and specifically highlight in the Discussion that comparing ex-vivo retinal to in-vivo cortical data is challenging. With these changes, we believe that the focus of the paper is explicitly defined to be on the neuronal representation of color in mouse visual cortex, rather than on the comparison of retinal and cortical color processing.

Limitations associated with ETA analysis One of the reviewers in the previous round of reviews raised the concern that the ETA analysis may not accurately capture responses of cells with nonlinear receptive field properties such as On/Off cells. This possibility and whether it is a concern should be discussed.

Thanks for this comment. We now discuss the limitation of using an ETA analysis in the

Discussion section.

Discrimination performance poor Discriminability of color or luminance is used as a measure of population coding. The discrimination performance appears to be quite poor - with 500-1000 neurons needed to reliably distinguish light from dark or green from UV. Intuitively I would expect that a single cell would provide such discrimination. Is this intuition wrong? If not, how do we interpret the discrimination analyses?

Thank you for raising this point. The plots in Fig. 2c (and Figs. 3-5) show discriminability in bits, with the discrimination accuracy in % highlighted by the dotted horizontal lines. For 500 neurons, the discriminability is approx. 0.8 bits, corresponding to 95% accuracy. Even for 50 neurons, the accuracy is significantly above chance level. We now mention in the legends that the dotted lines indicate decoding accuracy in %.

A simple camera could be positioned (perhaps attached to the head of the guitar) so as to view the hands moving over the fretboard. Perhaps visual methods which use commercial cameras to infer blood pressure could be used to estimate stress being applied by fingers [reference, reference]. Perhaps this would involve looking at changes in skin colour corresponding to blood flow restrictions resulting from stresses being applied. The apparatus described in this paper could be used to validate such an approach. Potentially the installation of a camera could potentially result in an apparatus more easily deployed at scale, and perhaps usable on many different instruments (without special fretboard modifications and such). Potentially it could also enable more dimensions of resolution, extending the one-dimensional limits of the described apparatus.

The term is Eulerian Video Magnification:

• https://www.youtube.com/watch?v=ONZcjs1Pjmk

Perhaps contemporary machine learning visual analysis could be applied also, and it would be potentially straightforward to record video data for training.

A more straightforward extension to the current study could be to apply visual analysis such that merely finger placements and gestures were identified to supplement the stress measurements. Indeed, visual analysis or motion capture approaches could be applied to video of the whole posture of the player for assessment of relationships between stress measurements across the fretboard and posture (such as sitting and standing), which can be significant.

Another complimentary measurement is audio. Stress/force sensor data could be supplemented with audio data analysis such as is employed by the likes of Yousician. A mentioned limitation of the apparatus is the measurement of vibrato effects/techniques. Could audio analysis supplement the existing apparatus's measuring capabilities to include such effects/techniques? Audio analysis can infer keys being typed on a keyboard, could it not also be used to infer frets being played, and with different forces applied?

Another form of sensor which may not have been considered is the Fiber Bragg Grating (FBG). Could this be feasible, perhaps in a specially-constructed fretboard? Would it add a greater resolution? Would it add a greater dimensionality to the stress measurements?

Author response:

The following is the response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

Nitta et al, in their manuscript titled, "Drosophila model to clarify the pathological significance of OPA1 in autosomal dominant optic atrophy." The novelty of this paper lies in its use of human (hOPA1) to try to rescue the phenotype of an OPA1 +/- Drosophilia DOA model (dOPA). The authors then use this model to investigate the differences between dominant-negative and haploinsufficient OPA1 variants. The value of this paper lies in the study of DN/HI variants rather than the establishment of the drosophila model per se as this has existed for some time and does have some significant disadvantages compared to existing models, particularly in the extra-ocular phenotype which is common with some OPA1 variants but not in humans. I judge the findings of this paper to be valuable with regards to significance and solid with regards to the strength of the evidence.

Suggestions for improvements:

(1) Stylistically the results section appears to have significant discussion/conclusion/inferences in section with reference to existing literature. I feel that this information would be better placed in the separate discussion section. E.g. lines 149-154.

We appreciate the reviewer’s suggestion to relocate the discussion, conclusions, and inferences, particularly those that reference existing literature, to a separate discussion section. For lines 149–154, we placed them in the discussion section (lines 343–347) as follows. “Our established fly model is the first simple organism to allow observation of degeneration of the retinal axons. The mitochondria in the axons showed fragmentation of mitochondria. Former studies have observed mitochondrial fragmentation in S2 cells (McQuibban et al., 2006), muscle tissue (Deng et al., 2008), segmental nerves (Trevisan et al., 2018), and ommatidia (Yarosh et al., 2008) due to the LOF of dOPA1.”

For lines 178–181, we also placed them in the discussion section (lines 347–351) as follows. “Our study presents compelling evidence that dOPA1 knockdown instigates neuronal degeneration, characterized by a sequential deterioration at the axonal terminals and extending to the cell bodies. This degenerative pattern, commencing from the distal axons and progressing proximally towards the cell soma, aligns with the paradigm of 'dying-back' neuropathy, a phenomenon extensively documented in various neurodegenerative disorders (Wang et al., 2012). ”

For lines 213–217, 218–220, and 222–223, we also placed them in the discussion section (lines 363– 391) as follows. “To elucidate the pathophysiological implications of mutations in the OPA1 gene, we engineered and expressed several human OPA1 variants, including the 2708-2711del mutation, associated with DOA, and the I382M mutation, located in the GTPase domain and linked to DOA. We also investigated the D438V and R445H mutations in the GTPase domain and correlated with the more severe DOA plus phenotype. The 2708-2711del mutation exhibited limited detectability via HA-tag probing. Still, it was undetectable with a myc tag, likely due to a frameshift event leading to the mutation's characteristic truncated protein product, as delineated in prior studies (Zanna et al., 2008). Contrastingly, the I382M, D438V, and R445H mutations demonstrated expression levels comparable to the WT hOPA1. However, the expression of these mutants in retinal axons did not restore the dOPA1 deficiency to the same extent as the WT hOPA1, as evidenced in Figure 5E. This finding indicates a functional impairment imparted by these mutations, aligning with established understanding (Zanna et al., 2008). Notably, while the 2708-2711del and I382M mutations exhibited limited functional rescue, the D438V and R445H mutations did not show significant rescue activity. This differential rescue efficiency suggests that the former mutations, particularly the I382M, categorized as a hypomorph (Del Dotto et al., 2018), may retain partial functional capacity, indicative of a LOF effect but with residual activity. The I382M missense mutation within the GTPase domain of OPA1 has been described as a mild hypomorph or a disease modifier. Intriguingly, this mutation alone does not induce significant clinical outcomes, as evidenced by multiple studies (Schaaf et al., 2011; Bonneau et al., 2014; Bonifert et al., 2014; Carelli et al., 2015). A significant reduction in protein levels has been observed in fibroblasts originating from patients harboring the I382M mutation. However, mitochondrial volume remains unaffected, and the fusion activity of mitochondria is only minimally influenced (Kane et al., 2017; Del Dotto et al., 2018). This observation is consistent with findings reported by de la Barca et al. in Human Molecular Genetics 2020, where a targeted metabolomics approach classified I382M as a mild hypomorph. In our current study, the I382M mutation preserves more OPA1 function compared to DN mutations, as depicted in Figures 5E and F. Considering the results from our Drosophila model and previous research, we hypothesize that the I382M mutation may constitute a mild hypomorphic variant. This might explain its failure to manifest a phenotype on its own, yet its contribution to increased severity when it occurs in compound heterozygosity.

(2) I do think further investigation as to why a reduction of mitochondria was noticed in the knockdown. There are conflicting reports on this in the literature. My own experience of this is fairly uniform mitochondrial number in WT vs OPA1 variant lines but with an increased level of mitophagy presumably reflecting a greater turnover. There are a number of ways to quantify mitochondrial load e.g. mtDNA quantification, protein quantification for tom20/hsp60 or equivalent. I feel the reliance on ICC here is not enough to draw conclusions. Furthermore, mitophagy markers could be checked at the same time either at the transcript or protein level. I feel this is important as it helps validate the drosophila model as we already have a lot of experimental data about the number and function of mitochondria in OPA+/- human/mammalian cells.

We thank the reviewer for the insightful comments and suggestions regarding our study on the impact of mitochondrial reduction in a knockdown model. We concur with the reviewer’s observation that our initial results did not definitively demonstrate a decrease in the number of mitochondria in retinal axons. Furthermore, we measured mitochondrial quantity by conducting western blotting using antiCOXII and found no reduction in mitochondrial content with the knockdown of dOPA1 (Figure S4A and B). Consequently, we have revised our manuscript to remove the statement “suggesting a decreased number of mitochondria in retinal axons. However, whether this decrease is due to degradation resulting from a decline in mitochondrial quality or axonal transport failure remains unclear.” Instead, we have refocused our conclusion to reflect our electron microscopy findings, which indicate reduced mitochondrial size and structural abnormalities. The reviewer’s observation of consistent mitochondrial numbers in WT versus mutant variant lines and elevated mitophagy levels prompted us to evaluate mitochondrial turnover as a significant factor in our study. Regarding verifying mitophagy markers, we incorporated the mito-QC marker in our experimental design. In our experiments, mito-QC was expressed in the retinal axons of Drosophila to assess mitophagy activity upon dOPA1 knockdown. We observed a notable increase in mCherry positive but GFP negative puncta signals one week after eclosion, indicating the activation of mitophagy (Figure 2D–H). This outcome strongly suggests that dOPA1 knockdown enhances mitophagy in our Drosophila model. The application of mito-QC as a quantitative marker for mitophagy, validated in previous studies, offers a robust approach to analyzing this process. Our findings elucidate the role of dOPA1 in mitochondrial dynamics and its implications for neuronal health. These results have been incorporated into Figure 2, with the corresponding text updated as follows (lines 159–167): “Given that an increase in mitophagy activity has been reported in mouse RGCs and nematode ADOA models (Zaninello et al., 2022; Zaninello et al., 2020), the mitoQC marker, an established indicator of mitophagy activity, was expressed in the photoreceptors of Drosophila. The mito-QC reporter consists of a tandem mCherry-GFP tag that localizes to the outer membrane of mitochondria (Lee et al., 2018). This construct allows the measurement of mitophagy by detecting an increase in the red-only mCherry signal when the GFP is degraded after mitochondria are transported to lysosomes. Post dOPA1 knockdown, we observed a significant elevation in mCherry positive and GFP negative puncta signals at one week, demonstrating an activation of mitophagy as a consequence of dOPA1 knockdown (Figure 2D–H).”  

(3) Could the authors comment on the failure of the dOPA1 rescue to return their biomarker, axonal number to control levels. In Figure 4D is there significance between the control and rescue. Presumably so as there is between the mutant and rescue and the difference looks less.

As the reviewer correctly pointed out, there is a significant difference between the control and rescue groups, which we have now included in the figure. Additionally, we have incorporated the following comments in the discussion section (lines 329–342) regarding this significant difference: “In our study, expressing dOPA1 in the retinal axons of dOPA1 mutants resulted in significant rescue, but it did not return to control levels. There are three possible explanations for this result. The first concerns gene expression levels. The Gal4-line used for the rescue experiments may not replicate the expression levels or timing of endogenous dOPA1. Considering that the optimal functionality of dOPA1 may be contingent upon specific gene expression levels, attaining a wild-type-like state necessitates the precise regulation of these expression levels. The second is a nonautonomous issue. Although dOPA1 gene expression was induced in the retinal axons for the rescue experiments, many retinal axons were homozygous mutants, while other cell types were heterozygous for the dOPA1 mutation. If there is a non-autonomous effect of dOPA1 in cells other than retinal axons, it might not be possible to restore the wild-type-like state fully. The third potential issue is that only one isoform of dOPA1 was expressed. In mouse OPA1, to completely restore mitochondrial network shape, an appropriate balance of at least two different isoforms, lOPA1 and s-OPA1, is required (Del Dotto et al., 2017). This requirement implies that multiple isoforms of dOPA1 are essential for the dynamic activities of mitochondria.”

(4) The authors have chosen an interesting if complicated missense variant to study, namely the I382M with several studies showing this is insufficient to cause disease in isolation and appears in high frequency on gnomAD but appears to worsen the phenotype when it appears as a compound het. I think this is worth discussing in the context of the results, particularly with regard to the ability for this variant to partially rescue the dOPA1 model as shown in Figure 5.

As the reviewer pointed out, the I382M mutation is known to act as a disease modifier. However, in our system, as suggested by Figure 5, I382M appears to retain more activity than DN mutations. Considering previous studies, we propose that I382M represents a mild hypomorph. Consequently, while I382M alone may not exhibit a phenotype, it could exacerbate severity in a compound heterozygous state. We have incorporated this perspective in our revised discussion (lines 375-391).

“Notably, while the 2708-2711del and I382M mutations exhibited limited functional rescue, the D438V and R445H mutations did not show significant rescue activity. This differential rescue efficiency suggests that the former mutations, particularly the I382M, categorized as a hypomorph (Del Dotto et al., 2018), may retain partial functional capacity, indicative of a LOF effect but with residual activity. The I382M missense mutation within the GTPase domain of OPA1 has been described as a mild hypomorph or a disease modifier. Intriguingly, this mutation alone does no induce significant clinical outcomes, as evidenced by multiple studies (Schaaf et al., 2011; Bonneau et al., 2014; Bonifert et al., 2014; Carelli et al., 2015). A significant reduction in protein levels has been observed in fibroblasts originating from patients harboring the I382M mutation. However, mitochondrial volume remains unaffected, and the fusion activity of mitochondria is only minimally influenced (Kane et al., 2017; Del Dotto et al., 2018). This observation is consistent with findings reported by de la Barca et al. in Human Molecular Genetics 2020, where a targeted metabolomics approach classified I382M as a mild hypomorph. In our current study, the I382M mutation preserves more OPA1 function compared to DN mutations, as depicted in Figures 5E and F. Considering the results from our Drosophila model and previous research, we hypothesize that the I382M mutation may constitute a mild hypomorphic variant. This might explain its failure to manifest a phenotype on its own, yet its contribution to increased severity when it occurs in compound heterozygosity.”

(5) I feel the main limitation of this paper is the reliance on axonal number as a biomarker for OPA1 function and ultimately rescue. I have concerns because a) this is not a well validated biomarker within the context of OPA1 variants b) we have little understanding of how this is affected by over/under expression and c) if it is a threshold effect e.g. once OPA1 levels reach <x% pathology develops but develops normally when opa1 expression is >x%. I think this is particularly relevant when the authors are using this model to make conclusions on dominant negativity/HI with the authors proposing that if expression of a hOPA1 transcript does not increase opa1 expression in a dOPA1 KO then this means that the variant is DN. The authors have used other biomarkers in parts of this manuscript e.g. ROS measurement and mito trafficking but I feel this would benefit from something else particularly in the latter experiments demonstrated in figure 5 and 6.

The reviewer raised concerns regarding the adequacy of axonal count as a validated biomarker in the context of OPA1 mutants. In response, we corroborated its validity using markers such as MitoSOX, Atg8, and COXII. Experiments employing MitoSOX revealed that the augmented ROS signals resulting from dOPA1 knockdown were mitigated by expressing human OPA1. Conversely, the mutant variants 2708-2711del, D438V, and R445H did not ameliorate these effects, paralleling the phenotype of axonal degeneration observed. These findings are documented in Figure 5F, and we have incorporated the following text into section lines 248–254 of the results:

“Furthermore, we assessed the potential for rescuing ROS signals. Similar to its effect on axonal degeneration, wild-type hOPA1 effectively mitigated the phenotype, whereas the 2708-2711del, D438V, and R445H mutants did not (Figure 5F). Importantly, the I382M variant also reduced ROS levels comparably to the wild type. These findings demonstrate that both axonal degeneration and the increase in ROS caused by dOPA1 downregulation can be effectively counteracted by hOPA1. Although I382M retains partial functionality, it acts as a relatively weak hypomorph in this experimental setup.”

Moreover, utilizing mito-QC, we observed elevated mitophagy in our Drosophila model, with these results now included in Figure 2D–H. Given the complexity of the genetics involved and the challenges in establishing lines, autophagy activity was quantified by comparing the ratio of Atg8-1 to Atg8-2 via Western blot analysis. However, no significant alterations were detected across any of the genotypes. Additionally, mitochondrial protein levels derived from COXII confirmed consistent mitochondrial quantities, showing no considerable variance following knockdown. These insights affirm that retinal axon degeneration and mitophagy activation are present in the Drosophila DOA model, although the Western blot analysis revealed no significant changes in autophagy activation. Such findings necessitate caution as this model may not fully replicate the molecular pathology of the corresponding human disease. These Western blot findings are presented in Figure S4, with the following addition made to section lines 255–263 of the results:

“We also conducted Western blot analyses using anti-COXII and anti-Atg8a antibodies to assess changes in mitochondrial quantity and autophagy activity following the knockdown of dOPA1. Mitochondrial protein levels, indicated by COXII quantification, were evaluated to verify mitochondrial content, and the ratio of Atg8a-1 to Atg8a-2 was used to measure autophagy activation. For these experiments, Tub-Gal4 was employed to systemically knockdown dOPA1. Considering the lethality of a whole-body dOPA1 knockdown, Tub-Gal80TS was utilized to repress the knockdown until eclosion by maintaining the flies at 20°C. After eclosion, we increased the temperature to 29°C for two weeks to induce the knockdown or expression of hOPA1 variants. The results revealed no significant differences across the genotypes tested (Figure S4A–D).”

In assessing the effects of dominant negative mutations, measurements including ROS levels, the ratio of Atg8-1 to Atg8-2, and the quantity of COXII protein were conducted, yet no significant differences were observed (Figure S6). This limitation of the fly model is mentioned in the results, noting the observation of the axonal degeneration phenotype but not alterations in ROS signaling, autophagy activity, or mitochondrial quantity as follows (line 287–290):

“We investigated the impacts of dominant negative mutations on mitochondrial oxidation levels, mitochondrial quantity, and autophagy activation levels; however, none of these parameters showed statistical significance (Figure S6).”

The reviewer also inquired about the effects of overexpressing and underexpressing OPA1 on axonal count and whether these effects are subject to a threshold. In response, we expressed both wild-type and variant forms of human OPA1 in Drosophila in vivo and assessed their protein levels using Western blot analysis. The results showed no significant differences in expression levels between the wild-type and variant forms in the OPA1 overexpression experiments, suggesting the absence of a variation threshold effect. These findings have been newly documented as quantitative data in Figure 5C. Furthermore, we have included a statement in the results section for Figure 6A, clarifying that overexpression of hOPA1 exhibited no discernible impact, as detailed on lines 274–276.

“The results presented in Figure 5C indicate that there are no significant differences in the expression levels among the variants, suggesting that variations in expression levels do not influence the outcomes.”

(6) Could the authors clarify what exons in Figure 5 are included in their transcript. My understanding is transcript NM_015560.3 contains exon 4,4b but not 5b. According to Song 2007 this transcript produces invariably s-OPA1 as it contains the exon 4b cleavage site. If this is true, this is a critical limitation in this study and in my opinion significantly undermines the likelihood of the proposed explanation of the findings presented in Figure 6. The primarily functional location of OPA1 is at the IMM and l-OPA1 is the primary opa1 isoform probably only that localizes here as the additional AA act as a IMM anchor. Given this is where GTPase likely oligomerizes the expression of s-OPA1 only is unlikely to interact anyway with native protein. I am not aware of any evidence s-OPA1 is involved in oligomerization. Therefore I don't think this method and specifically expression of a hOPA1 transcript which only makes s-OPA1 to be a reliable indicator of dominant negativity/interference with WT protein function. This could be checked by blotting UAS-hOPA1 protein with a OPA1 antibody specific to human OPA1 only and not to dOPA1. There are several available on the market and if the authors see only s-OPA1 then it confirms they are not expressing l-OPA1 with their hOPA1 construct.

As suggested by the reviewer, we performed a Western blot using a human OPA1 antibody to determine if the expressed hOPA1 was producing the l-OPA1 isoform, as shown in band 2 of Figure 5D. The results confirmed the presence of both l-OPA1 and what appears to be s-OPA1 in bands 2 and 4, respectively. These findings are documented in the updated Figure 5D, with a detailed description provided in the manuscript at lines 224-226. Additionally, the NM_015560.3 refers to isoform 1, which includes only exons 4 and 5, excluding exons 4b and 5b. This isoform can express both l-OPA1 and s-OPA1 (refer to Figure 1 in Song et al., J Cell Biol. 2007). We have updated the schematic diagram in the figure to include these exons. The formation of s-OPA1 through cleavage occurs at the OMA1 target site located in exon 5 and the Yme1L target site in exon 5b of OPA1. Isoform 1 of OPA1 is prone to cleavage by OMA1, but a homologous gene for OMA1 does not exist in Drosophila. Although a homologous gene for Yme1L is present in Drosophila, exon 5b is missing in isoform 1 of OPA1, leaving the origin of the smaller band resembling s-OPA1 unclear at this point.

Reviewer #2 (Public Review):

The data presented support and extend some previously published data using Drosophila as a model to unravel the cellular and genetic basis of human Autosomal dominant optic atrophy (DOA). In human, mutations in OPA1, a mitochondrial dynamin like GTPase (amongst others), are the most common cause for DOA. By using a Drosophila loss-of-function mutations, RNAi- mediated knockdown and overexpression, the authors could recapitulate some aspects of the disease phenotype, which could be rescued by the wild-type version of the human gene. Their assays allowed them to distinguish between mutations causing human DOA, affecting the optic system and supposed to be loss-of-function mutations, and those mutations supposed to act as dominant negative, resulting in DOA plus, in which other tissues/organs are affected as well. Based on the lack of information in the Materials and Methods section and in several figure legends, it was not in all cases possible to follow the conclusions of the authors.

We appreciate the reviewer's constructive feedback and the emphasis on enhancing clarity in our manuscript. We recognize the concerns raised about the lack of detailed information in the Materials and Methods section and several figure legends, which may have obscured our conclusions. In response, we have appended the detailed genotypes of the Drosophila strains used in each experiment to a supplementary table. Additionally, we realized that the description of 'immunohistochemistry and imaging' was too brief, previously referenced simply as “immunohistochemistry was performed as described previously (Sugie et al., 2017).” We have now expanded this section to include comprehensive methodological details. Furthermore, we have revised the figure legends to provide clearer and more thorough descriptions.

Similarly, how the knowledge gained could help to "inform early treatment decisions in patients with mutations in hOPA1" (line 38) cannot be followed.

To address the reviewer's comments, we have refined our explanation of the clinical relevance of our findings as follows. We believe this revision succinctly articulates the practical application of our research, directly responding to the reviewer’s concerns about linking the study's outcomes to treatment decisions for patients with hOPA1 mutations. By underscoring the model’s value in differential diagnosis and its influence on initiating treatment strategies, we have clarified this connection explicitly, within the constraints of the abstract’s word limit. The revised sentence now reads: "This fly model aids in distinguishing DOA from DOA plus and guides initial hOPA1 mutation treatment strategies."

Reviewer #3 (Public Review):

Nitta et al. establish a fly model of autosomal dominant optic atrophy, of which hundreds of different OPA1 mutations are the cause with wide phenotypic variance. It has long been hypothesized that missense OPA1 mutations affecting the GTPase domain, which are associated with more severe optic atrophy and extra-ophthalmic neurologic conditions such as sensorineural hearing loss (DOA plus), impart their effects through a dominant negative mechanism, but no clear direct evidence for this exists particularly in an animal model. The authors execute a well-designed study to establish their model, demonstrating a clear mitochondrial phenotype with multiple clinical analogs including optic atrophy measured as axonal degeneration. They then show that hOPA1 mitigates optic atrophy with the same efficacy as dOPA1, setting up the utility of their model to test disease-causing hOPA1 variants. Finally, they leverage this model to provide the first direct evidence for a dominant negative mechanism for 2 mutations causing DOA plus by expressing these variants in the background of a full hOPA1 complement.

Strengths of the paper include well-motivated objectives and hypotheses, overall solid design and execution, and a generally clear and thorough interpretation of their results. The results technically support their primary conclusions with caveats. The first is that both dOPA1 and hOPA1 fail to fully restore optic axonal integrity, yet the authors fail to acknowledge that this only constitutes a partial rescue, nor do they discuss how this fact might influence our interpretation of their subsequent results.

As the reviewer rightly points out, neither dOPA1 nor hOPA1 achieve a complete recovery. Therefore, we acknowledge that this represents only a partial rescue and have added the following explanations regarding this partial rescue in the results and discussion sections.

Result:

Significantly —> partially (lines 207 and 228) Discussion (lines 329–342):

In our study, expressing dOPA1 in the retinal axons of dOPA1 mutants resulted in significant rescue, but it did not return to control levels. There are three possible explanations for this result. The first concerns gene expression levels. The Gal4-line used for the rescue experiments may not replicate the expression levels or timing of endogenous dOPA1. Considering that the optimal functionality of dOPA1 may be contingent upon specific gene expression levels, attaining a wild-type-like state necessitates the precise regulation of these expression levels. The second is a non-autonomous issue. Although dOPA1 gene expression was induced in the retinal axons for the rescue experiments, many retinal axons were homozygous mutants, while other cell types were heterozygous for the dOPA1 mutation. If there is a non-autonomous effect of dOPA1 in cells other than retinal axons, it might not be possible to restore the wild-type-like state fully. The third potential issue is that only one isoform of dOPA1 was expressed. In mouse OPA1, to completely restore mitochondrial network shape, an appropriate balance of at least two different isoforms, l-OPA1 and s-OPA1, is required (Del Dotto et al., 2017). This requirement implies that multiple isoforms of dOPA1 are essential for the dynamic activities of mitochondria.

The second caveat is that their effect sizes are small. Statistically, the results indeed support a dominant negative effect of DOA plus-associated variants, yet the data show a marginal impact on axonal degeneration for these variants. The authors might have considered exploring the impact of these variants on other mitochondrial outcome measures they established earlier on. They might also consider providing some functional context for this marginal difference in axonal optic nerve degeneration.

In response to the reviewer’s comment regarding the modest effect sizes observed, we acknowledge that the magnitude of the reported changes is indeed small. To explore the impact of these variants on additional mitochondrial outcomes as suggested, we employed markers such as MitoSOX, Atg8, and COXII for validation. However, we could not detect any significant effects of the DOA plus-associated variants using these methods. We apologize for the redundancy, but to address Reviewer #1's fifth question, we present experimental results showing that while the increased ROS signals observed upon dOPA1 knockdown were rescued by expressing human OPA1, the mutant variants 2708-2711del, D438V, and R445H did not ameliorate this effect. This outcome mirrors the axonal degeneration phenotype and is documented in Figure 5F. The following text has been added to the results section lines 248–254:

“Furthermore, we assessed the potential for rescuing ROS signals. Similar to its effect on axonal degeneration, wild-type hOPA1 effectively mitigated the phenotype, whereas the 2708-2711del, D438V, and R445H mutants did not (Figure 5F). Importantly, the I382M variant also reduced ROS levels comparably to the wild type. These findings demonstrate that both axonal degeneration and the increase in ROS caused by dOPA1 downregulation can be effectively counteracted by hOPA1. Although I382M retains partial functionality, it acts as a relatively weak hypomorph in this experimental setup.”

Moreover, utilizing mito-QC, we observed elevated mitophagy in our Drosophila model, with these results now included in Figure 2D–H. Given the complexity of the genetics involved and the challenges in establishing lines, autophagy activity was quantified by comparing the ratio of Atg8-1 to Atg8-2 via Western blot analysis. However, no significant alterations were detected across any of the genotypes. Additionally, mitochondrial protein levels derived from COXII confirmed consistent mitochondrial quantities, showing no considerable variance following knockdown. These insights affirm that retinal axon degeneration and mitophagy activation are present in the Drosophila DOA model, although the Western blot analysis revealed no significant changes in autophagy activation. Such findings necessitate caution as this model may not fully replicate the molecular pathology of the corresponding human disease. These Western blot findings are presented in Figure S4, with the following addition made to section lines 255–263 of the results:

“We also conducted Western blot analyses using anti-COXII and anti-Atg8a antibodies to assess changes in mitochondrial quantity and autophagy activity following the knockdown of dOPA1. Mitochondrial protein levels, indicated by COXII quantification, were evaluated to verify mitochondrial content, and the ratio of Atg8a-1 to Atg8a-2 was used to measure autophagy activation. For these experiments, Tub-Gal4 was employed to systemically knockdown dOPA1. Considering the lethality of a whole-body dOPA1 knockdown, Tub-Gal80TS was utilized to repress the knockdown until eclosion by maintaining the flies at 20°C. After eclosion, we increased the temperature to 29°C for two weeks to induce the knockdown or expression of hOPA1 variants. The results revealed no significant differences across the genotypes tested (Figure S4A–D).”

In assessing the effects of dominant negative mutations, measurements including ROS levels, the ratio of Atg8-1 to Atg8-2, and the quantity of COXII protein were conducted, yet no significant differences were observed (Figure S6). This limitation of the fly model is mentioned in the results, noting the observation of the axonal degeneration phenotype but not alterations in ROS signaling, autophagy activity, or mitochondrial quantity as follows (line 287–290):

“We investigated the impacts of dominant negative mutations on mitochondrial oxidation levels, mitochondrial quantity, and autophagy activation levels; however, none of these parameters showed statistical significance (Figure S6).”

Despite these caveats, the authors provide the first animal model of DOA that also allows for rapid assessment and mechanistic testing of suspected OPA1 variants. The impact of this work in providing the first direct evidence of a dominant negative mechanism is under-stated considering how important this question is in development of genetic treatments for DOA. The authors discuss important points regarding the potential utility of this model in clinical science. Comments on the potential use of this model to investigate variants of unknown significance in clinical diagnosis requires further discussion of whether there is indeed precedent for this in other genetic conditions (since the model is nevertheless so evolutionarily removed from humans).

As suggested by the reviewer, we have expanded the discussion in our study to emphasize in greater detail the significance of the fruit fly model and the MeDUsA software we have developed, elaborating on the model's potential applications in clinical science and its precedents in other genetic disorders. Our text is as follows (lines 299–318):

“We have previously utilized MeDUsA to quantify axonal degeneration, applying this methodology extensively to various neurological disorders. The robust adaptability of this experimental system is demonstrated by its application in exploring a wide spectrum of genetic mutations associated with neurological conditions, highlighting its broad utility in neurogenetic research. We identified a novel de novo variant in Spliceosome Associated Factor 1, Recruiter of U4/U6.U5 Tri-SnRNP (SART1). The patient, born at 37 weeks with a birth weight of 2934g, exhibited significant developmental delays, including an inability to support head movement at 7 months, reliance on tube feeding, unresponsiveness to visual stimuli, and development of infantile spasms with hypsarrhythmia, as evidenced by EEG findings. Profound hearing loss and brain atrophy were confirmed through MRI imaging. To assess the functional impact of this novel human gene variant, we engineered transgenic Drosophila lines expressing both wild type and mutant SART1 under the control of a UAS promoter.

Our MeDUsA analysis suggested that the variant may confer a gain-of-toxic-function (Nitta et al.,  2023). Moreover, we identified heterozygous loss-of-function mutations in DHX9 as potentially causative for a newly characterized neurodevelopmental disorder. We further investigated the pathogenic potential of a novel heterozygous de novo missense mutation in DHX9 in a patient presenting with short stature, intellectual disability, and myocardial compaction. Our findings indicated a loss of function in the G414R and R1052Q variants of DHX9 (Yamada et al., 2023). This experimental framework has been instrumental in elucidating the impact of gene mutations, enhancing our ability to diagnose how novel variants influence gene function.”

Recommendations for the Authors:

Reviewer #1 (Recommendations For The Authors):

Overall I enjoyed reading this paper. It is well presented and represents a significant amount of well executed study. I feel it further characterizes a poorly understood model of OPA1 variants and one which displays significant differences with the human phenotype. However I feel the use of this model with the author's experiments are not enough to validate this model/experiment as a screening tool for dominant negativity. I have therefore suggested the above experiments as a way to both further validate the mitochondrial dysfunction in this model and to ensure that the expressed transcript is able affect oligomerization as this is a pre-requisite to the authors conclusions.

We assessed the extent to which our model reflects mitochondrial dysfunction using COXII, Atg8, and MitoSOX markers. Unfortunately, neither COXII levels nor the ratio of Atg8a-1 to Atg8a-2 showed significant variations across genotypes that would clarify the impact of dominant negative mutations. Nonetheless, MitoSOX and mito-QC results revealed that mitochondrial ROS levels and mitophagy are increased in Drosophila following intrinsic knockdown of dOPA1. These findings are documented in Figures 2, 5, and S6.

Regarding oligomer formation, the specifics remain elusive in this study. However, the expression of dOPA1K273A, identified as a dominant negative variant in Drosophila, significantly disrupted retinal axon organization, as detailed in Figure S7. From these observations, we hypothesize that oligomerization of wild-type and dominant negative forms in Drosophila results in axonal degeneration. Conversely, co-expression of Drosophila wild-type with human dominant negative forms does not induce degeneration, suggesting that they likely do not interact.

Reviewer #2 (Recommendations For The Authors):

Materials and Methods:

The authors used GMR-Gal4 to express OPA1-RNAi. I) GMR is expressed in most cells in the developing eye behind the morphogenetic furrow. So the defects observed can be due to knock- down in support cells rather than in photoreceptor cells.

We have added the following sentences in the result (lines 194–196)."The GMR-Gal4 driver does not exclusively target Gal4 expression to photoreceptor cells. Consequently, the observed retinal axonal degeneration could potentially be secondary to abnormalities in support cells external to the photoreceptors.”

OPA1-RNAi: how complete is the knock-down? Have the authors tested more than one RNAi line?

We conducted experiments with an additional RNAi line, and similarly observed degeneration in the retinal axons (Figure S2 A and B; lines 178–179).

The loss-of-function allele, induced by a P-element insertion, gives several eye phenotypes when heterozygous (Yarosh et al., 2008). Does RNAi expression lead to the same phenotypes?

A previous report indicated that the compound eyes of homozygous mutations of dOPA1 displayed a glossy eye phenotype (Yarosh et al., 2008). Upon knocking down dOPA1 using the GMR-Gal4 driver, we also observed a glossy eye-like rough eye phenotype in the compound eyes. These findings have been added to Figure S3 and lines 192–194.

There is no description on the way the somatic clones were generated. How were mutant cells in clones distinguished from wild-type cells (e. g. in Fig. 4).

In the Methods section, we described the procedure for generating clones and their genotypes as follows (lines 502–505): "The dOPA1 clone analysis was performed by inducing flippase expression in the eyes using either ey-Gal4 with UAS-flp or ey3.5-flp, followed by recombination at the chromosomal location FRT42D to generate a mosaic of cells homozygous for dOPA1s3475." Furthermore, we have created a table detailing these genotypes. In these experiments, it was not possible to differentiate between the clone and WT cells. Accordingly, we have noted in the Results section (lines 201–203): "Note that the mutant clone analysis was conducted in a context where mutant and heterozygous cells coexist as a mosaic, and it was not possible to distinguish between them.”

Why were flies kept at 29{degree sign}C? this is rather unusual.

Increased temperature was demonstrated to induce elevated expression of GAL4 (Kramer and Staveley, Genet. Mol. Res., 2003), which in turn led to an enhanced expression of the target genes. Therefore, experiments involving knockdown assays or Western blotting to detect human OPA1 protein were exclusively conducted at 29°C. However, all other experiments were performed at 25°C, as described in the methods sections: “Flies were maintained at 25°C on standard fly food. For knockdown experiments (Figures 1C–E, 1F–H, 2A–H, 3B–K, 5F, S1, S2 A and B, and S6A), flies were kept at 29°C in darkness.” Furthermore, “We regulated protein expression temporally across the whole body using the Tub-Gal4 and Tub-GAL80TS system. Flies harboring each hOPA1 variant were maintained at a permissive temperature of 20°C, and upon emergence, females were transferred to a restrictive temperature of 29°C for subsequent experiments.”

Legends:

It would be helpful to have a description of the genotypes of the flies used in the different experiments. This could also be included as a table.

We have created a table detailing the genotypes. Additionally, in the legend, we have included a note to consult the supplementary table for genotypes.

Results:

Line 141: It is not clear what they mean by "degradation", is it axonal degeneration? And if so, what is the argument for this here?

In the manuscript, we addressed the potential for mitochondrial degradation; however, recognizing that the expression was ambiguous, the following sentence has been omitted: "Nevertheless, the degradation resulting from mitochondrial fragmentation may have decreased the mitochondrial signal.”

Fig. 2: Axons of which photoreceptors are shown?

We have added "a set of the R7/8 retinal axons" to the legend of Figure 2.

Line 167: The authors write that axonal degeneration is more severe after seven days than after eclosion. Is this effect light-dependent? The same question concerns the disappearance of the rhabdomere (Fig. 3G–J).

We conducted the experiments in darkness, ensuring that the observed degeneration is not light- dependent. This condition has been added to the methods section to clarify the experimental conditions.

Line 178/179: Based on what results do they conclude that there is degeneration of the "terminals" of the axons?

Quantification via MeDUsA has enabled us to count the number of axonal terminals, and a noted decrease has led us to conclude axonal terminal degeneration. We have published two papers on these findings. We have added the following description to the results section to clarify how we defined degeneration (lines 174–176): "We have assessed the extent of their reduction from the total axonal terminal count, thereby determining the degree of axonal terminal degeneration (Richard JNS 2022; Nitta HMG 2023).

Line 189: They write: ".. we observed dOPA1 mutant axons...". How did they distinguish es mutant from the controls?

Fig. 5 and Fig. 6: How did they distinguish genetically mutant cells from genetically control cells in the somatic clones?

Mutant clone analysis was conducted in a context where mutant and heterozygous cells coexist as a mosaic, and it was not possible to distinguish between them. Accordingly, this point has been added to lines 201–203, “Note that the mutant clone analysis was conducted in a context where mutant and heterozygous cells coexist as a mosaic, and it was not possible to distinguish between them.” and the text in the results section has been modified as follows:

(Before “To determine if dOPA1 is responsible for axon neurodegeneration, we observed the dOPA1 mutant axons by expressing full- length versions of dOPA1 in the photoreceptors at one day after eclosion and found that dOPA1 expression significantly rescued the axonal degeneration” —>

(After “To determine if dOPA1 is responsible for axon neurodegeneration, we quantify the number of the axons in the dOPA1 eye clone fly with the expression of dOPA1 at one day after eclosion and found that dOPA1 expression partially rescued the axonal degeneration”

Line 225/226: It is not clear to me how their approach "can quantitatively measure the degree of LOF".

To address the reviewer's question and clarify how our approach quantitatively measures the degree of loss of function (LOF), we revised the statement (lines 238–247):

"Our methodology distinctively facilitates the quantitative evaluation of LOF severity by comparing the rescue capabilities of various mutations. Notably, the 2708-2711del and I382M mutations demonstrated only partial rescue, indicative of a hypomorphic effect with residual activity. In contrast, the D438V and R445H mutations failed to show significant rescue, suggesting a more profound LOF. The correlation between the partial rescue by the 2708-2711del and I382M mutations and their classification as hypomorphic is significant. Moreover, the observed differences in rescue efficacy correspond to the clinical severities associated with these mutations, namely in DOA and DOA plus disorders. Thus, our results substantiate the model’s ability to quantitatively discriminate among mutations based on their impact on protein functionality, providing an insightful measure of LOF magnitude.”

Discussion:

Line 251, 252 and line 358: What is "the optic nerve" in the adult Drosophila?

In humans, the axons of retinal ganglion cells (RGCs) are referred to as the optic nerve, and we posit that the retinal axons in flies are similar to this structure. In the introduction section, where it is described that the visual systems of flies and humans bear resemblance, we have appended the following definition (lines 107–108): “In this study, we defined the retinal axons of Drosophila as analogous to the human optic nerve.”

Line 344: These bands appear only upon overexpression of the hOPA1 constructs, so this part of the is very speculative.

Confirmation was achieved using anti-hOPA1, demonstrating that myc is not nonspecific. These results have been added to Figure 5D. Furthermore, the phrase “The upper band was expected as” has been revised to “From a size perspective, the upper band was inferred to represent the full-length hOPA1 including the mitochondria import sequence (MIS).” (lines 464–465)

I was missing a discussion about the increase of ROS upon loss/reduction of dOPA1 observed by others and described here. Is there an increase of ROS upon expression of any of the constructs used?

We demonstrated that not only axonal degeneration but also ROS can be suppressed by expressing human OPA1 in the genetic background of dOPA1 knockdown. Additionally, rescue was not possible with any variants except for I382M. Furthermore, we assessed whether there were changes in ROS in the evaluation of dominant negatives, but no significant differences were observed in this experimental system. These findings have been added to the discussion section as follows (lines 318–328). “Our research established that dOPA1 knockdown precipitates axonal degeneration and elevates ROS signals in retinal axons. Expression of human OPA1 within this context effectively mitigated both phenomena; it partially reversed axonal degeneration and nearly completely normalized ROS levels. These results imply that factors other than increased ROS may drive the axonal degeneration observed post-knockdown. Furthermore, while differences between the impacts of DN mutations and loss-of- function mutations were evident in axonal degeneration, they were less apparent when using ROS as a biomarker. The extensive use of transgenes in our experiments might have mitigated the knockdown effects. In a systemic dOPA1 knockdown, assessments of mitochondrial quantity and autophagy activity revealed no significant changes, suggesting that the cellular consequences of reduced OPA1 expression might vary across different cell types.”

Reviewer #3 (Recommendations For The Authors):

Consider being more explicit regarding literature that has or has failed to test a direct dominant negative effect by expressing a variant in question in the background of a full OPA1 complement. My understanding is that this is the first direct evidence of this widely held hypothesis. This lends to the main claim promoting the utility of fly as a model in general. The authors might also outline this in the introduction as a knowledge gap they fill through this study.

In the introduction, we have incorporated a passage that highlights precedents capable of distinguishing between LOF and DN effects, and we note the absence of models capable of dissecting these distinctions within an in vivo organism. This study aims to address this gap, proposing a model that elucidates the differential impacts of LOF and DN within the context of a living model organism, thereby contributing to a deeper understanding of their roles in disease pathology. We added the following sentences in the introduction (lines 71–80).

“In the quest to differentiate between LOF and DN effects within the context of genetic mutations, precedents exist in simpler systems such as yeast and human fibroblasts. These models have provided valuable insights into the conserved functions of OPA1 across species, as evidenced by studies in yeast models (Del Dotto et al., 2018) and fibroblasts derived from patients harboring OPA1 mutations (Kane et al., 2017). However, the ability to distinguish between LOF and DN effects in an in vivo model organism, particularly at the structural level of retinal axon degeneration, has remained elusive. This gap underscores the necessity for a more complex model that not only facilitates molecular analysis but also enables the examination of structural changes in axons and mitochondria, akin to those observed in the actual disease state.”

The authors should clarify the language used in the abstract and introduction on the effect of hOPA1 DOA and DOA plus on the dOPA1- phenotype. Currently written as "none of the previously reports mutations known to cause DOA or DOA plus were rescued, their functions seems to be impaired." but presumably the authors mean that these variants failed to rescue to the dOPA1 deficient phenotype.

We thank the reviewer for the constructive feedback. We acknowledge the need for clarity in our description of the effects of hOPA1 DOA and DOA plus mutations on the dOPA1- phenotype in both the abstract and the introduction. The current phrasing, "none of the previously reported mutations known to cause DOA or DOA plus were rescued, their functions seem to be impaired," may indeed be confusing. To address your concern, we have revised this statement to more accurately reflect our findings: "Previously reported mutations failed to rescue the dOPA1 deficiency phenotype." For Abstract site, we have changed as following. "we could not rescue any previously reported mutations known to cause either DOA or DOA plus.”→ “mutations previously identified did not ameliorate the dOPA1 deficiency phenotype.”

DOA plus is associated with a multiple sclerosis-like illness; as written it suggests that the pathogenesis of sporadic multiple sclerosis and that associated with DOA plus share and underlying pathogenic mechanism. Please use the qualifier "-like illness." 

We have added the term “multiple sclerosis-like illness” wherever “multiple sclerosis” is mentioned.

Author response:

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

Public Reviews:  

Reviewer #1 (Public Review):  

Summary:  

Heer and Sheffield used 2 photon imaging to dissect the functional contributions of convergent dopamine and noradrenaline inputs to the dorsal hippocampus CA1 in head-restrained mice running down a virtual linear path. Mice were trained to collect water rewards at the end of the track and on test days, calcium activity was recorded from dopamine (DA) axons originating in the ventral tegmental area (VTA, n=7) and noradrenaline axons from the locus coeruleus (LC, n=87) under several conditions. When mice ran laps in a familiar environment, VTA DA axons exhibited ramping activity along the track that correlated with distance to reward and velocity to some extent, while LC input activity remained constant across the track, but correlated invariantly with velocity and time to motion onset. A subset of recordings taken when the reward was removed showed diminished ramping activity in VTA DA axons, but no changes in the LC axons, confirming that DA axon activity is locked to reward availability. When mice were subsequently introduced to a new environment, the ramping to reward activity in the DA axons disappeared, while LC axons showed a dramatic increase in activity lasting 90 s (6 laps) following the environment switch. In the final analysis, the authors sought to disentangle LC axon activity induced by novelty vs. behavioral changes induced by novelty by removing periods in which animals were immobile and established that the activity observed in the first 2 laps reflected novelty-induced signal in LC axons.  

Strengths:  

The results presented in this manuscript provide insights into the specific contributions of catecholaminergic input to the dorsal hippocampus CA1 during spatial navigation in a rewarded virtual environment, offering a detailed analysis of the resolution of single axons. The data analysis is thorough and possible confounding variables and data interpretation are carefully considered.  

Weaknesses:  

Aspects of the methodology, data analysis, and interpretation diminish the overall significance of the findings, as detailed below.  

The LC axonal recordings are well-powered, but the DA axonal recordings are severely underpowered, with recordings taken from a mere 7 axons (compared to 87 LC axons).

Additionally, 2 different calcium indicators with differential kinetics and sensitivity to calcium changes (GCaMP6S and GCaMP7b) were used (n=3, n=4 respectively) and the data pooled. This makes it very challenging to draw any valid conclusions from the data, particularly in the novelty experiment. The surprising lack of novelty-induced DA axon activity may be a false negative. Indeed, at least 1 axon (axon 2) appears to be showing a novelty-induced rise in activity in Figure 3C. Changes in activity in 4/7 axons are also referred to as a 'majority' occurrence in the manuscript, which again is not an accurate representation of the observed data.  

We appreciate the reviewer's detailed feedback regarding the analysis of VTA axons in our dataset. The relatively low sample size for VTA axons is due to their sparsity in the dCA1 region of the hippocampus and the inherent difficulty in recording from these axons. VTA axons are challenging to capture due to their low baseline fluorescence and long-range axon segments, resulting in a typical yield of only a single axon per field of view (FOV) per animal. In contrast, LC axons are more abundant in dCA1.

To address the disparity in sample sizes between LC and VTA axons, we down-sampled the LC axons to match the number of VTA axons, repeating this process 1000 times to create a distribution. However, we acknowledge the reviewer's concern that the relatively low sample size for VTA axons might result in insufficient sampling of this population. Increasing the baseline expression of GCaMP to record from VTA axons requires several months, limiting our ability to quickly expand the sample size.

In response to the reviewer's comments, we have added recordings from 2 additional VTA axons, increasing the sample size from 7 to 9. We re-analyzed all data from the familiar environment with n=9 VTA axons, comparing them to down-sampled LC axons as previously described. However, the additional axons were not recorded in the novel environment. We agree with the reviewer that the lack of novelty-induced DA axon activity may be a false negative. To address this, we have revised the description of our results to include the following sentence:

“However, 1 VTA ROI showed an increase in activity immediately following exposure to novelty, indicating heterogeneity across VTA axons in CA1, and the lack of a novelty signal on average may be due to a small sample size.”

Regarding the use of two different GCaMP constructs, we understand the reviewer's concern. We used GCaMP6s and GCaMP7b variants to determine if one would improve the success rate of recording from VTA axons. Given the long duration of these experiments and the low yield, we pooled the data from both GCaMP variants to increase statistical power. However, we recognize the importance of verifying that there are no differences in the signals recorded with these variants.

With the addition of 2 VTA DA axons expressing GCaMP6s, we now have n=5 GCaMP6s and n=4 GCaMP7b VTA DA axons. This allowed us to compare the activity of the two sensors in the familiar environment. As shown in new Supplementary Figure 2, both sets of axons responded similarly to the variables measured: position in VR, time to motion onset, and animal velocity (although the GCaMP6s expressing axons showed stronger correlations). Since all LC axons recorded expressed GCaMP6s, we also specifically compared VTA GCaMP6s axons to LC GCaMP6s axons (Supp Fig. 3). Our conclusions remained consistent when comparing this subset of VTA axons to LC axons.

Overall, our paper now includes comparisons of combined VTA axons (n=9) and separately the GCaMP6s-expressing VTA axons (n=5) with LC axons. Both datasets support our initial conclusions that VTA axons signal proximity to reward, while LC axons encode velocity and motion initiation in familiar environments.

The authors conducted analysis on recording data exclusively from periods of running in the novelty experiment to isolate the effects of novelty from novelty-induced changes in behavior. However, if the goal is to distinguish between changes in locus coeruleus (LC) axon activity induced by novelty and those induced by motion, analyzing LC axon activity during periods of immobility would enhance the robustness of the results.  

We appreciate the reviewer's insightful suggestion to analyze LC axon activity during periods of immobility to distinguish between changes induced by novelty and those induced by motion. This additional analysis would indeed strengthen our conclusions regarding the LC novelty signal.

In response to this suggestion, we performed the same analysis as before, but focused on periods of immobility. Our findings indicate that following exposure to novelty, there was a significant increase in LC activity specifically during immobility. This supports the idea that LC axons produce a novelty signal that is independent of novelty-induced behavioral changes. The results of this analysis are now presented in new Supplementary Figure 5b

The authors attribute the ramping activity of the DA axons to the encoding of the animals' position relative to reward. However, given the extensive data implicating the dorsal CA1 in timing, and the remarkable periodicity of the behavior, the fact that DA axons could be signalling temporal information should be considered.  

This is an insightful comment regarding the potential role of VTA DA axons in signaling temporal information. We agree that VTA DA axons could indeed be encoding temporal information, as previous work from our lab has shown that these axons exhibit ramping activity when averaged by time to reward (Krishnan et al., 2022).

To address this, we have now examined DA axon activity relative to time to reward, as shown in new Supplementary Figure 4. Our analysis confirms that these axons ramp up in activity relative to time to reward. Given the periodicity of our mice's behavior in these experiments, as the reviewer correctly points out, we are unable to distinguish between spatial proximity to reward and time to reward. We have added a sentence to our paper highlighting this limitation and stating that further experiments are necessary to differentiate these two variables.

Krishnan, L.S., Heer, C., Cherian, C., Sheffield, M.E. Reward expectation extinction restructures and degrades CA1 spatial maps through loss of a dopaminergic reward proximity signal. Nat Commun 13, 6662 (2022).

The authors should explain and justify the use of a longer linear track (3m, as opposed to 2m in the DAT-cre mice) in the LC axon recording experiments.  

We appreciate the reviewer's insightful comment regarding the use of a longer linear track (3m, as opposed to 2m in the DAT-cre mice) in the LC axon recording experiments. The choice of a 3m track for LC axon recordings was made to align with a previous experiment from our lab (Dong et al., 2021), in which mice were exposed to a novel 3m track while CA1 pyramidal cell populations were recorded. In that study, we detailed the time course of place field formation within the novel track. Our current hypothesis is that LC axons signal novelty, and we aimed to investigate whether the time course of LC axon activity aligns with the time course of place field formation. This hypothesis, and the potential role of LC axons in facilitating plasticity for new place field formation, is further discussed in the Discussion section of our paper.

For the VTA axon recordings, we utilized a 2m track, consistent with another recent study from our lab (Krishnan et al., 2022), where reward expectation was manipulated, and CA1 pyramidal cell populations were recorded. By matching the track length to this prior study, we aimed to explore how VTA dopaminergic inputs to CA1 might influence CA1 population dynamics along the track under conditions of varying reward expectations.

We acknowledge that using different track lengths for LC and VTA recordings introduces a variable that could potentially confound direct comparisons. To address this, we normalized the track lengths for our LC versus VTA comparison analysis. This normalization allowed us to directly compare patterns of activity across the two types of axons by adjusting the data to a common scale, thereby ensuring that any observed differences or similarities are attributable to the intrinsic properties of the axons rather than differences in track lengths. By doing so, we could assess relative changes in activity levels at matched spatial bins.

Although the experiences of the animals on the different track lengths are not identical, our observations suggest that LC and VTA axon signals are not majorly influenced by variations in track length. LC axons are associated with velocity and a pre-motion initiation signal, neither of which are affected by track length. VTA axons, which also correlate with velocity, can be compared to LC axon velocity signals because mice reach maximal velocity very quickly a long the track, well before the end of the 2m track. The range of velocities are therefore capture on both track lengths. While VTA axons exhibit ramping activity as they approach the reward zone—a signal potentially modulated by track length—LC axons do not show such ramping to reward signals. Thus, a comparison across different track lengths is justified for this aspect of our analysis.

To further enhance the rigor of our comparisons between axon dynamics recorded on 2m and 3m tracks, we conducted an additional analysis plotting axon activity by time to reward and actual (un-normalized) distance from reward (Supplementary Figure 4). This analysis revealed very similar signals between the two sets of axons, supporting our initial conclusions.

We thank the reviewer for raising this important point and hope that our detailed explanation and additional analysis address their concern.

Krishnan, L.S., Heer, C., Cherian, C., Sheffield, M.E. Reward expectation extinction restructures and degrades CA1 spatial maps through loss of a dopaminergic reward proximity signal. Nat Commun 13, 6662 (2022).

Dong, C., Madar, A. D. & Sheffield, M.E. Distinct place cell dynamics in CA1 and CA3 encode experience in new environments. Nat Commun 12, 2977 (2021).

Reviewer #2 (Public Review):  

Summary:  

The authors used 2-photon Ca2+-imaging to study the activity of ventral tegmental area (VTA) and locus coeruleus (LC) axons in the CA1 region of the dorsal hippocampus in head-fixed male mice moving on linear paths in virtual reality (VR) environments.  

The main findings were as follows:  

- In a familiar environment, the activity of both VTA axons and LC axons increased with the mice's running speed on the Styrofoam wheel, with which they could move along a linear track through a VR environment.  

- VTA, but not LC, axons showed marked reward position-related activity, showing a ramping-up of activity when mice approached a learned reward position.  

- In contrast, the activity of LC axons ramped up before the initiation of movement on the Styrofoam wheel.  

- In addition, exposure to a novel VR environment increased LC axon activity, but not VTA axon activity.  

Overall, the study shows that the activity of catecholaminergic axons from VTA and LC to dorsal hippocampal CA1 can partly reflect distinct environmental, behavioral, and cognitive factors. Whereas both VTA and LC activity reflected running speed, VTA, but not LC axon activity reflected the approach of a learned reward, and LC, but not VTA, axon activity reflected initiation of running and novelty of the VR environment.  

I have no specific expertise with respect to 2-photon imaging, so cannot evaluate the validity of the specific methods used to collect and analyse 2-photon calcium imaging data of axonal activity.  

Strengths:  

(1) Using a state-of-the-art approach to record separately the activity of VTA and LC axons with high temporal resolution in awake mice moving through virtual environments, the authors provide convincing evidence that the activity of VTA and LC axons projecting to dorsal CA1 reflect partly distinct environmental, behavioral and cognitive factors.  

(2) The study will help a) to interpret previous findings on how hippocampal dopamine and norepinephrine or selective manipulations of hippocampal LC or VTA inputs modulate behavior and b) to generate specific hypotheses on the impact of selective manipulations of hippocampal LC or VTA inputs on behavior.  

Weaknesses:  

(1) The findings are correlational and do not allow strong conclusions on how VTA or LC inputs to dorsal CA1 affect cognition and behavior. However, as indicated above under Strengths, the findings will aid the interpretation of previous findings and help to generate new hypotheses as to how VTA or LC inputs to dorsal CA1 affect distinct cognitive and behavioral functions.  

(2) Some aspects of the methodology would benefit from clarification.  

First, to help others to better scrutinize, evaluate, and potentially to reproduce the research, the authors may wish to check if their reporting follows the ARRIVE (Animal Research: Reporting of In Vivo Experiments) guidelines for the full and transparent reporting of research involving animals (https://arriveguidelines.org/). For example, I think it would be important to include a sample size justification (e.g., based on previous studies, considerations of statistical power, practical considerations, or a combination of these factors). The authors should also include the provenance of the mice. Moreover, although I am not an expert in 2-photon imaging, I think it would be useful to provide a clearer description of exclusion criteria for imaging data.

We thank the reviewer for helping us formalize the scientific rigor of our study. There are ten ARRIVE Guidelines and we have addressed most of them in our study already. However, there is an opportunity to add detail. We have listed below all ten points and how we have addressed each one (and point out any new additions):

(1) Experimental design - we go into great depth explaining the experimental set-up, how we used the autofluorescent blebs as imaging controls, how we controlled for different sample sizes between the two populations, and the statistical tests used for comparisons. We also carefully accounted for animal behavior when quantifying and describing axon dynamics both in the familiar and novel environments.

(2) Sample size - we state both the number of ROIs and mice for each analysis. We have now also added the number of mice we observed specific types of activity in. 

(3) Inclusion/exclusion criteria - The following has now been added to the Methods section: Out of the 36 NET-Cre mice injected, 15 were never recorded from for either failing to reach behavioral criteria, or a lack of visible expression in axons. Out of the 54 DAT-Cre mice injected, imaging was never conducted in 36 of them for lack of expression or failing to reach behavioral criteria. Out of the remaining 21 NET-CRE, 5 were excluded for heat bubbles, z-drift, or bleaching, while 10 DAT-Cre were excluded for the same reasons. This was determined by visually assessing imaging sessions, followed by using the registration metrics output by suite2p. This registration metric conducted a PCA on the motion-corrected ROIs and plotted the first PC. If the PC drifted largely, to the point where no activity was apparent, the video was excluded from analysis. 

(4) Randomization - Already included in the paper is a description of random downsampling of LC axons to make statistical comparisons with VTA axons. LC axons were selected pseudo-randomly (only one axon per imaging session) to match VTA sampling statistics. This randomization was repeated 1000 times and comparisons were made against this random distribution. 

(5) Blinding-masking - no blinding/masking was conducted as no treatments were given that would require this. We will include this statement in the next version. 

(6) Outcomes - We defined all outcomes measured, such as those related to animal behavior and axon signaling. 

(7) Statistical methods - None of the reviewers had any issues regarding our description of statistical methods, which we described in great detail in this version of the paper. 

(8) Experimental animals - We have now described that DAT- Cre mice were obtained through JAX labs, and NET-Cre mice were obtained from the Tonegawa lab (Wagatsuma et al. 2017). This was absent in the initial version of the paper.

(9) Experimental procedure - Already listed in great detail in Methods section.

(10) Results - Rigorously described in detail for behaviors and related axon dynamics.

Wagatsuma, Akiko, Teruhiro Okuyama, Chen Sun, Lillian M. Smith, Kuniya Abe, and Susumu Tonegawa. “Locus Coeruleus Input to Hippocampal CA3 Drives Single-Trial Learning of a Novel Context.” Proceedings of the National Academy of Sciences 115, no. 2 (January 9, 2018): E310–16. https://doi.org/10.1073/pnas.1714082115.

Second, why were different linear tracks used for studies of VTA and LC axon activity (from line 362)? Could this potentially contribute to the partly distinct activity correlates that were found for VTA and LC axons?  

We thank the reviewer for pointing this out and giving us a chance to address it directly. A detailed response to this is written above for a similar comment from reviewer 1.

Third, the authors seem to have used two different criteria for defining immobility. Immobility was defined as moving at <5 cm/s for the behavioral analysis in Figure 3a, but as <0.2 cm/s for the imaging data analysis in Figure 4 (see legends to these figures and also see Methods, from line 447, line 469, line 498)? I do not understand why, and it would be good if the authors explained this.  

This is a typo leftover from before we converted velocity from rotational units of the treadmill to cm/s. This has now been corrected.

(3) In the Results section (from line 182) the authors convincingly addressed the possibility that less time spent immobile in the novel environment may have contributed to the novelty-induced increase of LC axon activity in dorsal CA1 (Figure 4). In addition, initially (for the first 2-4 laps), the mice also ran more slowly in the novel environment (Figure 3aIII, top panel). Given that LC and VTA axon activity were both increasing with velocity (Figure 1F), reduced velocity in the novel environment may have reduced LC and VTA axon activity, but this possibility was not addressed. Reduced LC axon activity in the novel environment could have blunted the noveltyinduced increase. More importantly, any potential novelty-induced increase in VTA axon activity could have been masked by decreases in VTA axon activity due to reduced velocity. The latter may help to explain the discrepancy between the present study and previous findings that VTA neuron firing was increased by novelty (see Discussion, from line 243). It may be useful for the authors to address these possibilities based on their data in the Results section, or to consider them in their Discussion.  

We appreciate the reviewer's insightful comment regarding the potential impact of decreased velocity on novelty responses in LC and VTA axons. The decreased velocity in the novel environment could lead to a diminished novelty response in LC axons and could mask a subtle novelty signal in VTA axons. We have now included the following points in our discussion:

“In addition, as noted above, on average we did observe a velocity associated signal in VTA axons. When mice were exposed to the novel environment their velocity initially decreased. This would be expected to reduce the average signal across the VTA axon population relative to the higher velocity in the familiar environment. It is possible that this decrease could somewhat mask a subtle novelty induced signal in VTA axons. Therefore, additional experiments should be conducted to investigate the heterogeneity of these axons and their activity under different experimental conditions during tightly controlled behavior.”

“As discussed above, the slowing down of animal behavior in the novel environment could have decreased LC axon activity and reduced the magnitude of the novelty signal we detected during running. The novelty signal we report here may therefore be an under estimate of it's magnitude under matched behavioral settings.”

However, it is important to note that although VTA axons, on average, showed activity modulated by velocity in a familiar rewarded environment, this relationship was largely due to the activity of two VTA axons that were strongly modulated by velocity, indicating heterogeneity within the VTA axon population in dCA1. We have highlighted this point in the discussion. We also discuss that:

“It is possible that some VTA DA inputs to dCA1 respond to novel environments, and the small number of axons recorded here are not representative of the whole population.”

(4) Sensory properties of the water reward, which the mice may be able to detect, could account for reward-related activity of VTA axons (instead of an expectation of reward). Do the authors have evidence that this is not the case? Occasional probe trials, intermixed with rewarded trials, could be used to test for this possibility.  

Mice receive their water reward through a water spout that is immobile and positioned directly in front of their mouth. Water delivery is triggered by a solenoid when the mice reach the end of the virtual track. Therefore, because the water spout is immobile and the water reward is not delivered until they reach the end of the track, there is nothing for the mice to detect during their run. We have added clarifications about the water spout to the Methods and Results sections, along with appropriate discussion points.

Additionally, we note that the ramping activity of VTA axons is still present on the initial laps with no reward (Krishnan et al., 2022), indicating that this activity is not directly related to the presence or absence of water but is instead associated with the animal’s reward expectation.

We thank the reviewer for raising this point and hope that these clarifications address their concern.

Reviewer #3 (Public Review):  

Summary:  

Heer and Sheffield provide a well-written manuscript that clearly articulates the theoretical motivation to investigate specific catecholaminergic projections to dorsal CA1 of the hippocampus during a reward-based behavior. Using 2-photon calcium imaging in two groups of cre transgenic mice, the authors examine the activity of VTA-CA1 dopamine and LC-CA1 noradrenergic axons during reward seeking in a linear track virtual reality (VR) task. The authors provide a descriptive account of VTA and LC activities during walking, approach to reward, and environment change. Their results demonstrate LC-CA1 axons are activated by walking onset, modulated by walking velocity, and heighten their activity during environment change. In contrast, VTA-CA1 axons were most activated during the approach to reward locations. Together the authors provide a functional dissociation between these catecholamine projections to CA1. A major strength of their approach is the methodological rigor of 2-photon recording, data processing, and analysis approaches. These important systems neuroscience studies provide solid evidence that will contribute to the broader field of learning and memory. The conclusions of this manuscript are mostly well supported by the data, but some additional analysis and/or experiments may be required to fully support the author's conclusions.  

Weaknesses:  

(1) During teleportation between familiar to novel environments the authors report a decrease in the freezing ratio when combining the mice in the two experimental groups (Figure 3aiii). A major conclusion from the manuscript is the difference in VTA and LC activity following environment change, given VTA and LC activity were recorded in separate groups of mice, did the authors observe a similar significant reduction in freezing ratio when analyzing the behavior in LC and VTA groups separately?  

In response to the comment regarding the freezing ratios during teleportation between familiar and novel environments, we have analyzed the freezing ratios and lap velocities of DAT-Cre and NET-Cre mice separately (Fig. 3Aiii). Our analysis shows that the mean lap velocities of both groups overlap in the familiar environment and significantly decrease on the first lap of the novel environment (Fig. 3iii, top). For subsequent laps, the velocities in both groups are not statistically significantly different from the familiar environment lap velocities.

Freezing ratios also show a statistically significant decrease on the first lap of the novel environment compared to the familiar environment in both groups (Fig. 3iii, bottom). In the NETCRE mice, the freezing ratios remain statistically lower in subsequent laps, while in the DATCRE mice, the following laps show a similar trend but without statistical significance. This lack of statistical significance in the DAT-CRE mice is likely due to their already lower freezing ratios in the familiar environment. Overall, the data demonstrate similar behavioral responses in the two groups of mice during the switch from the familiar to the novel environment.

(2) The authors satisfactorily apply control analyses to account for the unequal axon numbers recorded in the LC and VTA groups (e.g. Figure 1). However, given the heterogeneity of responses observed in Figures 3c, 4b and the relatively low number of VTA axons recorded (compared to LC), there are some possible limitations to the author's conclusions. A conclusion that LC-CA1 axons, as a general principle, heighten their activity during novel environment presentation, would require this activity profile to be observed in some of the axons recorded in most all LC-CA1 mice.

We agree with the reviewer’s point. To address this issue, when downsampling LC axons to compare to VTA axons, we matched the sampling statistics of the VTA axons/mice by only selecting one LC axon from each mouse to match the VTA dataset.

Additionally, we have now included the number of recording sessions and the number of mice in which we observed each type of activity. This information has been added to further clarify and support our conclusions.

Additionally, if the general conclusion is that VTA-CA1 axons ramp activity during the approach to reward, it would be expected that this activity profile was recorded in the axons of most all VTA-CA1 mice. Can the authors include an analysis to demonstrate that each LC-CA1 mouse contained axons that were activated during novel environments and that each VTA-CA1 mouse contained axons that ramped during the approach to reward?  

As above, we have now added the number of mice that had each activity type we report in the paper here.  

(3) A primary claim is that LC axons projecting to CA1 become activated during novel VR environment presentation. However, the experimental design did not control for the presentation of a familiar environment. As I understand, the presentation order of environments was always familiar, then novel. For this reason, it is unknown whether LC axons are responding to novel environments or environmental change. Did the authors re-present the familiar environment after the novel environment while recording LC-CA1 activity?  

While we did not vary the presentation order of familiar and novel environments, we recorded the activity of LC axons in some mice when exposed to a dark environment (no VR cues) prior to exposure to the familiar environment. Our analysis of this data demonstrates that LC axons are also active following abrupt exposure to the familiar environment.

We have added a new figure showing this response (Supplementary Figure 5A) and expanded on our original discussion point that LC axon activity generally correlates with arousal, as this result also supports that interpretation.

We thank the reviewer for highlighting this important consideration. It certainly helps with the interpretation regarding what LC axons generally encode.  

>Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):  

In addition to what has been described in the public review, I have the following recommendations:  

The sample size of DA axon recordings should be increased with the use of a single GCaMP for valid conclusions to be made about the lack of novelty-inducted activity in these axons.  

We have increased the n of VTA GCaMP6s axons in the familiar environment by including two axons that were recorded in the familiar rewarded condition. We have also conducted an analysis comparing GCaMPs versus GCaMP7b, which is discussed in detail above.

Regarding the concerns about valid conclusions of novelty-induced activity in VTA axons, we have added a comment in the discussion to tone down our conclusions regarding the lack of a novelty signal in the VTA axons. This valid concern is discussed in detail above.  

The title is currently very generic, and non-informative. I recommend the use of more specific language in describing the type of behavior under investigation. It is not clear to the reviewer why 'learning' is included here.  

Original title: “Distinct catecholaminergic pathways projecting to hippocampal CA1 transmit contrasting signals during behavior and learning”

To make it more specific to the experiments conducted here, we have changed the title to this:

New title: “Distinct catecholaminergic pathways projecting to hippocampal CA1 transmit contrasting signals during navigation in familiar and novel environments”

Error noted in Figure 4C legend - remove reference to VTA ROIs.  

The reference to VTA ROIs has been removed from the figure legend

Reviewer #2 (Recommendations For The Authors):  

(1) The concluding sentence of the Abstract could be more specific: which distinct types of information are reflected/'signaled'/'encoded' by LC and VTA inputs to dorsal CA1?  

The abstract has been adjusted accordingly. The new sentence is more specific: “These inputs encode unique information, with reward information in VTA inputs and novelty and kinematic information in LC inputs, likely contributing to differential modulation of hippocampal activity during behavior and learning.”

(2) Line 46/47: The study by Mamad et al. (2017) did not quite show that VTA dopamine input to dorsal CA1 'drives place preference'. To my understanding, the study showed that suppression of VTA dopamine signaling in a specific place caused avoidance of this place and that VTA dopamine signaling modulated hippocampal place-related firing. So, please consider rephrasing.  

Corrected, thanks for pointing this out.

(3) Legend to Figure 3AIII: 'Each lap was compared to the first lap in F . . .' Could you clarify if 'F' refers to the 'familiar environment?  

Figure legend has been changed accordingly

(4) Line 176: '36 LC neurons' - should this not be '36 imaged axon terminals in dorsal CA1' or something along these lines?  

This reference has been changed to “LC axon ROIs”

(5) Line 353: Why was water restriction started before the hippocampal window implant, if behavioral training to run for water reward only started after the implant? Please clarify.

A sentence was added to the methods to explain that this was done to reduce bleeding and swelling during the hippocampal window implantation.  

(6) Line 377: '. . . which took 10-14 days (although some mice never reached this threshold).' How many mice did not reach the criterion within 14 days? I think it is not accurate to say the mice 'never' reached the threshold, as they were only tested for a limited period of time.  

We have added details of how many mice were excluded from each group and the reason why they were excluded.

(7) Exclusion criteria for imaging data: The authors state (from line 402): 'Imaging sessions with large amounts of drift or bleaching were excluded from analysis (8 sessions for NET mice, 6 sessions for LC Mice).' What exactly were the quantitative exclusion criteria? Were these defined before the onset of the study or throughout the study?  

Imaging sessions were first qualitatively assessed by looking for disappearance or movement of structures in the Z-plane throughout the imaging FOV. Additionally, following motion correction in suite2p, we used the registration metrics, which plots the first Principle Component of the motion corrected images, to assess for drift, bleaching, or heat bubbles. If this variable increased or decreased greatly throughout a session, to the point where any apparent activity was not visible in the first PC, the dataset was excluded. We have added these exclusion criteria to the methods section.

Reviewer #3 (Recommendations For The Authors):  

Please provide a justification or rationale for having two different criteria for immobility (< 5cm/sec) and freezing (<0.2 cm/sec). If VTA and LC axon activities are different between these two velocities, please provide some commentary on this difference.  

This is a typo leftover from before we converted velocity from rotational units to cm/s.

Reviewer #1 (Public Review):

Summary:

Heer and Sheffield used 2 photon imaging to dissect the functional contributions of convergent dopamine and noradrenaline inputs to the dorsal hippocampus CA1 in head restrained mice running down a virtual linear path. Mice were trained to collect water reward at the end of the track and on test days, calcium activity was recorded from dopamine (DA) axons originating in ventral tegmental area (VTA, n=7) and noradrenaline axons from the locus coeruleus (LC, n=87) under several conditions. When mice ran laps in a familiar environment, VTA DA axons exhibited ramping activity along the track that correlated with distance to reward and velocity to some extent, while LC input activity remained constant across the track, but correlated invariantly with velocity and time to motion onset. A subset of recordings taken when the reward was removed showed diminished ramping activity in VTA DA axons, but no changes in the LC axons, confirming that DA axon activity is locked to reward availability. When mice were subsequently introduced to a new environment, the ramping to reward activity in the DA axons disappeared, while LC axons showed a dramatic increase in activity lasting 90s (6 laps) following the environment switch. In the final analysis, the authors sought to disentangle LC axon activity induced by novelty vs. behavioral changes induced by novelty by removing periods in which animals were immobile and established that the activity observed in the first 2 laps reflected novelty-induced signal in LC axons.

The revised manuscript included additional evidence of increased (but transient) signal in LC axons after a transition to a novel environment during periods of immobility, and also that a change from dark to familiar environment induces a peak in LC axon activity, showing that LC input to dCA1 may not solely signal novelty.

Strengths:

The results presented in this manuscript provide insights into the specific contributions of catecholaminergic input to the dorsal hippocampus CA1 during spatial navigation in a rewarded virtual environment, offering a detailed analysis at the resolution of single axons. The data analysis is thorough and possible confounding variables and data interpretation are carefully considered.

The authors have addressed my concerns in a thorough manner. The reviewer also appreciates the increased transparency of reporting in the revised manuscript.

Weaknesses:

Listed below are some remaining comments.<br /> The increase in LC activity with any change in environment (from familiar to novel or from dark to familiar) suggests that LC input acts not solely as a novelty signal, but as a general arousal or salience signal in response to environmental changes. Based on this, I have a couple of questions:

• Is the overall claim that LC input to the dHC signals novelty still valid based on observed findings - as claimed throughout the manuscript?<br /> • Would the omission of a reward be considered a salient change in the environment that activates LC signals, or is the LC not involved with processing reward-related information? Has the activity of LC and VTA axons been analysed in the seconds following reward presentation and/or omission?

Reviewer #2 (Public Review):

Summary:

The authors used 2-photon Ca2+-imaging to study the activity of ventral tegmental area (VTA) and locus coeruleus (LC) axons in the CA1 region of the dorsal hippocampus in head-fixed male mice moving on linear paths in virtual reality (VR) environments.

The main findings were as follows:<br /> - In a familiar environment, activity of both VTA axons and LC axons increased with the mice's running speed on the Styrofoam wheel, with which they could move along a linear track through a VR environment.<br /> - VTA, but not LC, axons showed marked reward position-related activity, showing a ramping-up of activity when mice approached a learned reward position.<br /> - In contrast, activity of LC axons ramped up before initiation of movement on the Styrofoam wheel.<br /> - In addition, exposure to a novel VR environment increased LC axon activity, but not VTA axon activity.

Overall, the study shows that the activity of catecholaminergic axons from VTA and LC to dorsal hippocampal CA1 can partly reflect distinct environmental, behavioral and cognitive factors. Whereas both VTA and LC activity reflected running speed, VTA, but not LC axon activity reflected the approach of a learned reward and LC, but not VTA, axon activity reflected initiation of running and novelty of the VR environment.

I have no specific expertise with respect to 2-photon imaging, so cannot evaluate the validity of the specific methods used to collect and analyse 2-photon calcium imaging data of axonal activity.

Strengths:

(1) Using a state-of-the-art approach to record separately the activity of VTA and LC axons with high temporal resolution in awake mice moving through virtual environments, the authors provide convincing evidence that activity of VTA and LC axons projecting to dorsal CA1 reflect partly distinct environmental, behavioral and cognitive factors.

(2) The study will help a) to interpret previous findings on how hippocampal dopamine and norepinephrine or selective manipulations of hippocampal LC or VTA inputs modulate behavior and b) to generate specific hypotheses on the impact of selective manipulations of hippocampal LC or VTA inputs on behavior.

Weaknesses:

(1) The findings are correlational and do not allow strong conclusions on how VTA or LC inputs to dorsal CA1 affect cognition and behavior. However, as indicated above under Strengths, the findings will aid the interpretation of previous findings and help to generate new hypotheses as to how VTA or LC inputs to dorsal CA1 affect distinct cognitive and behavioral functions.

(2) Some aspects of the methodology would benefit from clarification.<br /> First, to help others to better scrutinize, evaluate and potentially to reproduce the research, the authors may wish to check if their reporting follows the ARRIVE (Animal Research: Reporting of In Vivo Experiments) guidelines for the full and transparent reporting of research involving animals (https://arriveguidelines.org/). For example, I think it would be important to include a sample size justification (e.g., based on previous studies, considerations of statistical power, practical considerations or a combination of these factors). The authors should also include the provenance of the mice. Moreover, although I am not an expert in 2-photon imaging, I think it would be useful to provide a clearer description of exclusion criteria for imaging data (see below, Recommendations for the authors).<br /> Second, why were different linear tracks used for studies of VTA and LC axon activity (from line 362)? Could this potentially contribute to the partly distinct activity correlates that were found for VTA and LC axons?<br /> Third, the authors seem to have used two different criteria for defining immobility. Immobility was defined as moving at <5 cm/s for the behavioral analysis in Fig. 3a, but as <0.2 cm/s for the imaging data analysis in Fig. 4 (see legends to these figures and also see Methods, from line 447, line 469, line 498)? I do not understand why, and it would be good if the authors explained this.

(3) In the Results section (from line 182) the authors convincingly addressed the possibility that less time spent immobile in the novel environment may have contributed to the novelty-induced increase of LC axon activity in dorsal CA1 (Fig. 4). In addition, initially (for the first 2-4 laps), the mice also ran more slowly in the novel environment (Fig. 3aIII, top panel). Given that LC and VTA axon activity were both increasing with velocity (Fig. 1F), reduced velocity in the novel environment may have reduced LC and VTA axon activity, but this possibility was not addressed. Reduced LC axon activity in the novel environment could have blunted the novelty-induced increase. More importantly, any potential novelty-induced increase in VTA axon activity could have been masked by decreases in VTA axon activity due to reduced velocity. The latter may help to explain the discrepancy between the present study and previous findings that VTA neuron firing was increased by novelty (see Discussion, from line 243). It may be useful for the authors to address these possibilities based on their data in the Results section, or to consider them in their Discussion.

(4) Sensory properties of the water reward, which the mice may be able to detect, could account for reward-related activity of VTA axons (instead of an expectation of reward). Do the authors have evidence that this is not the case? Occasional probe trials, intermixed with rewarded trials, could be used to test for this possibility.

REVIEW OF THE REVISED MANUSCRIPT<br /> I thank the authors for their responses addressing some of the weaknesses I raised in my original comments.

Regarding their clarification of some methodological issues [Point 2) above], I have a few additional comments:<br /> - I appreciate that the authors clearly state the sample sizes contributing to the data. However, sample size justifications (e.g. based on previous studies, considerations of statistical power, practical considerations or a combination of these factors) are still lacking.<br /> - It is good that the authors have now clearly indicated how many mice they excluded due to lack of GCaMP expression or due to failure to reach the behavioral criteria. They also indicated that they discarded some of the collected datasets, based on the visual assessment of imaging sessions and the registration metrics output by suite2p. I appreciate that this may be common practice (although I am not using 2-photon imaging myself). However, I note that to minimize the risk of experimenter bias and improve reproducibility, it would be preferable to have more clearly defined quantitative criteria for such exclusions.<br /> - The authors clarified in their response why they used two different linear tracks for their studies of VTA and LC axon activity. I would encourage them to include this clarification in the manuscript. From the authors' response, I understand that they chose the different track lengths to facilitate comparison to previous studies involving LC and VTA axon recordings. However, given that the present paper aimed to compare LC and VTA axon recordings, the use of different track lengths for LC and VTA axon recordings remains a limitation of the present paper.

• NOT: 4, 8, 15
• ?: 7

• : 1, 3, 5, 6, 13

• = *

Reviewer #3 (Public Review):

Summary:

The authors performed wide-field and 2-photon imaging in vivo in awake head-fixed mice, to compare receptive fields and tonotopic organization in thalamocortical recipient (TR) neurons vs corticothalamic (CT) neurons of mouse auditory cortex. TR neurons were found in all cortical layers while CT neurons were restricted to layer 6. The TR neurons at nominal depths of 200-400 microns have a remarkable degree of tonotopy (as good if not better than tonotopic maps reported by multiunit recordings). In contrast, CT neurons were very heterogenous in terms of their best frequency (BF), even when focusing on the low vs high-frequency regions of the primary auditory cortex. CT neurons also had wider tuning.

Strengths:

This is a thorough examination using modern methods, helping to resolve a question in the field with projection-specific mapping.

Weaknesses:

There are some limitations due to the methods, and it's unclear what the importance of these responses are outside of behavioral context or measured at single timepoints given the plasticity, context-dependence, and receptive field 'drift' that can occur in the cortex.

(1) Probably the biggest conceptual difficulty I have with the paper is comparing these results to past studies mapping auditory cortex topography, mainly due to differences in methods. Conventionally, the tonotopic organization is observed for characteristic frequency maps (not best frequency maps), as tuning precision degrades and the best frequency can shift as sound intensity increases. The authors used six attenuation levels (30-80 dB SPL) and reported that the background noise of the 2-photon scope is <30 dB SPL, which seems very quiet. The authors should at least describe the sound-proofing they used to get the noise level that low, and some sense of noise across the 2-40 kHz frequency range would be nice as a supplementary figure. It also remains unclear just what the 2-photon dF/F response represents in terms of spikes. Classic mapping using single-unit or multi-unit electrodes might be sensitive to single spikes (as might be emitted at characteristic frequency), but this might not be as obvious for Ca2+ imaging. This isn't a concern for the internal comparison here between TR and CT cells as conditions are similar, but is a concern for relating the tonotopy or lack thereof reported here to other studies.

(2) It seems a bit peculiar that while 2721 CT neurons (N=10 mice) were imaged, less than half as many TR cells were imaged (n=1041 cells from N=5 mice). I would have expected there to be many more TR neurons even mouse for mouse (normalizing by number of neurons per mouse), but perhaps the authors were just interested in a comparison data set and not being as thorough or complete with the TR imaging?

(3) The authors' definitions of neuronal response type in the methods need more quantitative detail. The authors state: ""Irregular" neurons exhibited spontaneous activity with highly variable responses to sound stimulation. "Tuned" neurons were responsive neurons that demonstrated significant selectivity for certain stimuli. "Silent" neurons were defined as those that remained completely inactive during our recording period (> 30 min). For tuned neurons, the best frequency (BF) was defined as the sound frequency associated with the highest response averaged across all sound levels.". The authors need to define what their thresholds are for 'highly variable', 'significant', and 'completely inactive'. Is best frequency the most significant response, the global max (even if another stimulus evokes a very close amplitude response), etc.

First test for the RL policy was to beat the SL Policy.

6

Author response:

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

eLife assessment

In this fundamental study, the authors use innovative fine-scale motion capture technologies to study visual vigilance with high-acuity vision, to estimate the visual fixation of free-feeding pigeons. The authors present convincing evidence for use of the fovea to inspect predator cues, the behavioral state influencing the latency for fovea use, and the use of the fovea decreasing the latency to escape of both the focal individual and other flock members. The work will be of broad interest to behavioral ecologists.

We thank the editor for his interest and feedback on the manuscript. We hereafter addressed the comments of the reviewer.

Reviewer #1 (Public Review):

Summary:

The authors were using an innovative technic to study the visual vigilance based on high-acuity vision, the fovea. Combining motion-capture features and visual space around the head, the authors were able to estimate the visual fixation of free-feeding pigeon at any moment. Simulating predator attacks on screens, they showed that 1) pigeons used their fovea to inspect predators cues, 2) the behavioural state (feeding or head-up) influenced the latency to use the fovea and 3) the use of the fovea decrease the latency to escape of both the individual that foveate the predators cues but also the other flock members.

Strengths:

The paper is very interesting, and combines innovative technic well adapted to study the importance of high-acuity vision for spotting a predator, but also of improving the behavioural response (escaping). The results are strong and the models used are well-adapted. This paper is a major contribution to our understanding of the use of visual adaptation in a foraging context when at risk. This is also a major contribution to the understanding of individual interaction in a flock.

Weaknesses:

I have identified only two weaknesses:

(1) The authors often mixed the methods and the results, Which reduces the readability and fluidity of the manuscript. I would recommend the authors to re-structure the manuscript.<br /> (2) In some parts, the authors stated that they reconstructed the visual field of the pigeon, which is not true. They identified the foveal positions, but not the visual fields, which involve different sectors (binocular, monocular or blind). Similarly, they sometimes mix-up the area centralis and the fovea, which are two different visual adaptations.

Thank you for your positive feedback. We addressed these comments by restructuring the methods and result sections as suggested, and by checking the terminology and specific vocabulary used throughout the manuscript.

Reviewer #1 (Recommendations For The Authors):

First, I would like to say that I really enjoyed the manuscript. This is a great contribution to the field.

Thank you for the positive feedback, we highly appreciate it.

Then, I have some comments that I hope, would help the authors to improve the manuscript.

Major comments :

I would recommend the authors to restructure the methods and the results section. In many parts, the models used are presented in the results section, while this should be presented in the methods section.

Thank you for the suggestion, we now have ensured that the model descriptions are presented in the statistic section of the methods.

To me, the introduction is too long (more than 5 pages). It would be beneficial to reduce it considerably. Furthermore, in the introduction, it misses some information about the visual abilities of your species ((visual acuity, visual field, temporal resolution, contrast sensitivity....).

We agree that the introduction was very long and reduced it by removing the “Methodological issues” as well as strongly reducing the “Experimental rationales” to a minimum. We also added the missing information on the visual abilities of the pigeons in the “Experimental rationales” section (see L135-150). Please note, however, that we refer to the temporal resolution of pigeon vision in the method section, to associate it with the information of the used monitor’s resolution.

Minor comments :

Lines 37-39: This needs a reference.

A reference has been added (McFarland, 1977)

Lines 39-41: But see some papers published recently on Harris's hawks.

Thank you for the references, we added the citation as well as a few more papers (Kane et al., 2015; Kano et al., 2018; Miñano et al., 2023; Yorzinski & Platt, 2014).

Lines 41-43: This sentence needs a reference as well.

A reference has been added (Cresswell, 1994; M. H. R. Evans et al., 2018; Inglis & Lazarus, 1981)

Lines 56-103: In this paragraph, head down and head up also depends from the retinal map of the birds! Some birds have visual streak that allow them to see a potential threats while foraging. Please add more information about the importance of photoreceptors distribution.

Thank you for pointing out this issue. We rewrote the sentence L65-69 as follows to include the importance retinal structures.

“In several species, especially those with a broad visual field and specific retinal structures such as the visual streaks, individuals can simultaneously engage in foraging activities while remaining vigilant (Fernández-Juricic, 2012), likely using peripheral vision to detect approaching threats (Bednekoff & Lima, 2005; Cresswell et al., 2003; Kaby & Lind, 2003; Lima & Bednekoff, 1999).”

Lines 76-79: you wrote : ".... favor alternative hypotheses based on their findings". Which findings? You need to explain.

We rewrote this part as follows (L80-81).

“other studies found evidence for the risk dilution (Beauchamp & Ruxton, 2008) and the edge effect (Inglis & Lazarus, 1981) in their study systems.”

Lines 109-110: It would be good to have a representation of what is an area and a fovea, and how it is placed in the eye, what type of fovea exists and how it is related to visual field. Where does it project?

We now give a better description of the pigeon’s visual field in the experimental rationales section that we hope will help the reader understanding the key features of pigeon’s vision (see L135-150). Specifically, we now say in L137-138:

“they have one fovea centrally located in the retina of each eye, with an acuity of 12.6 c/deg (Hodos et al., 1985). Their fovea projects laterally at ~75° into the horizon in their visual field.”

Lines 109-113: You might need to see some new papers here about the fovea. See for instance Bringmann 2019.

Thank you for the suggestion, we now give a more precise definition of the fovea and refer to Bringmann’s paper for more details (L113-114):

“a pit-like area in the retina with high concentration of cone cells where visual acuity is highest, and is responsible for sharp, detailed, and color vision.”

Lines 113-120: Please explain how the visual field is related to fovea? Where is the fovea project in the visual fields?

Similarly to the question above, we now give a more precise description of the pigeon’s visual field (see L135-150).

Line 131-134: For a non-expert, you would need to explain what is micro, meso and macro scale?

These sentences have been removed when shortening the introduction and we are not referring to micro, meso and macro scales anymore.

Lines 134-136: Please explain in one sentence the technique here.

We now explain in one sentence how motion capture enables the tracking of head and body orientation (L130-132):

“Motion capture cameras track with high accuracy the 3D position of markers, which, when attached to the pigeon’s head and body, enables to reconstruct the rotations of the head and body in all directions.”

Line 140: You presented here for the first time the word "foveation". Has this term been used before? If so, please add a reference. If not, please explain what you mean by foveation precisely.

Thank you for noticing this lack. We are now providing the following definition “directing visual focus to the fovea to achieve the clearest vision” in the first place where we mention the term foveation (L149-150).

Lines 146-148: Please explain why this proves that it is appropriate to not record eyes movements, and is this true for every behaviours?

We acknowledge that some small eye movement might occur and reduce the accuracy of the method. This error is considered in the system using the +-10 degrees range around the foveas. The lines the reviewer referred to were removed when shortening the introduction, but we added an explanation in the paragraph describing pigeon vision to make it clearer (L147-150):

“Yet, it should be noted that their eye movement was not tracked in our system, although it is typically confined within a 5 degrees range (Wohlschläger et al., 1993). We thus considered this estimation error of the foveation (directing visual focus to the fovea to achieve the clearest vision) in our analysis, as a part of the error margin (see Methods).”

Lines 161-163: What is the frontal and binocular field for? You would need to explain the different fields of view and what they are supposed to be for.

Furthermore, does the visual field of pigeon have been studied? If so, you would need to add more information about it.

This information is now given in the new paragraph describing the pigeon’s vision in the  “Experimental rationales” section (see L135-150).

Figure 1: It is not clear here which panels correspond to a, b or c. Please use some boxes to clarify it.

Thank you for the comment, we now have made the figure’s sub-panels clearer.

Lines 193-194: You wrote "... such as foveas (also known as the area centralis). No, this is not the same.

(1) In some species, you have two foveas, one placed centrally in the retina, one place temporally. So the fovea is not the area centralis.

(2) Second, some species do have an area centralis but without a fovea.

Thank you for pointing out the inaccuracy. In this case, we were referring specifically to the pigeon’s fovea which is sometimes referred to as “area centralis”, but we now changed the sentence as follow to avoid any confusion (L174-175):

“The initial two hypotheses (Hypotheses 1 and 2) aim to examine whether foveation correlates with predator detection.”

Lines 192-212: I did not understand the logic of the hypotheses numbers? Why do you have 2.1 but not 3.1 for instance? And if you have two hypotheses for the within a global one (for instance, 2.1 and 2.2), what is the main hypothesis 2? You should explain more here because we get lost here and in the result section as well.

We recognize this section might have appeared confusing to the reader. In short, we had four main hypotheses: 1) the fovea is used to evaluate predator cues, 2) the latency to foveate is related to vigilance behaviors. These first 2 hypotheses aimed to determine if the latency to foveate on the predator cue could be related to the detection. 3) foveation is related to the escape response of the pigeons and 4) there is a collective influence in the escape response. We further divided some of the hypotheses into 2 sub-hypotheses whenever 2 different tests were used to answer the same question. We have modified this section to be clearer.

Lines 224-229: Where are the figures and statistics for these results?

These results are presented in Table S1. We apologize for forgetting to add this reference and have now added it (L211).

Lines 229-231: This should be in the method section.

This model explanation (as well as all other hereafter mentioned) have been moved to the method section as suggested.

Lines 248-252: This should be in the method section. Furthermore, you should better explain the model selection.

Please see earlier comment. Additionally, we are now better explaining how the model has been built.

Figure 2: It is not clear on the figure which letters correspond to which panels. Please improve the readability of the figure.

It was modified accordingly.

Lines 274-278: This should be in the method section.

Please see earlier comment.

Line 281: The "Fig.3" should be mentioned in the previous sentence.

It was modified accordingly.

Figure 3: Please explain why the latency to foveate had negative values in Fig.2 but not here, and not in Fig. 4 as well. This again highlights that we missed a number of information in the methods about the transformation of the data and the model selection.

The variable presented in Fig 2d is not the latency to foveate but the “Normalized frequency at which the object was observed within foveal regions” (hypothesis 1). It represents the amount of time the object was lying within one of the foveal regions of the individual (“how long the pigeons foveated on it”), further normalized to unit sum to make all objects comparable. This variable was indeed logit-transformed (hence the negative value) to improve residual fit in the model, but this information (as well as other transformations) are always clearly stated on the axis caption of the graphs. Additionally, we now have improved the statistical analysis section to make the model used for each hypothesis testing clearer. But please let us know if you have suggestions for a further improvement in terms of presentation.

Lines 297-301: This should be in the method section.

Please see earlier comment.

Lines 301-305: Fig. 3 b and c only referred to the two first factors. Please add more figures for the other factors. This could be in supp. Mat.

We added the 3 graphs for the proportion of time foveating on the monitor, the saccade rate and the proportion of time foveating on conspecifics in the supplementary (Fig S6).

Lines 306-309: This should be in methods, and you should have explained in methods how you performed your model selection.....

We prefer leaving this paragraph in the result section, as it was intended to give the reader extra information on the predictive power of the different variables (by comparing the effectiveness of the models including one variable at a time, all the rest being equal) and not on the model selection per se. However, we now explain our goal better in the statistics section regarding this analysis (L635-636):

“We further tested the relative predictive power of the different test variables by comparing the resulting models’ efficiency using AIC scores.”

Lines 317-319: This should be in the method section.

Please see earlier comment.

Lines 320-322: This should be in the method section.

Please see earlier comment.

Lines 332-334: This should be in the method section.

Please see earlier comment.

Lines 334-336: Then, if this is not significant, you cannot say that.

Thank you for noticing the inaccuracy, we have now rephrased it as (L298-299):

“Earlier foveation of the first pigeon was not significantly related to an earlier escape responses among the other flock members, although there was a trend (χ2(1) = 3.66, p = 0.0559).”

Line 336: Please explain why you did different models. We missed a lot of information in the method about your strategy for statistics.?

We have now added a lot more information on the models in the statistics section, according to this comment as well as the previous ones. We hope the explanations of the analyses are now clearer to the reader.

Lines 339-349: This should be in the method section.

Please see earlier comment.

Results section: As you may have understood, there are too many sentence that should be moved into the method section. Futhermore, I would recommend to modify the headdings so that they are more biologically speaking. Similarly to what you have done in the discussion section.

Thank you for the comments. We agree with most of them, and have modified the manuscript accordingly. Additionally, we now use the same headings in the results section as the ones used in the discussion to make the text easier to follow.

Lines 500-501: What were the body weight of the pigeon? At which weight of their full weight they were?

This information is now added (492 ± 41g; mean ± SD). We did not control the amount of food during our experiments and only ensured 24h without food by feeding the pigeons after the experiment was completed. This information was added as follows (L454-456):

“On experimental days, they were fed only after the experiments was completed; this ensures 24-hour no feeding at the time of the experiment, although we did not control the amount of the food over the course of the experimental periods.”

Line 522-523: Those screens are very good for pigeons.

Thank you for the positive comment, we indeed tried to match bird vision as close as possible.

Lines 527-528: At which frequency was produced the moving stimulus? Your screen can display up to 144Hz, which is very good. But can your laptop do it? If not, it is important to mention it as pigeons may have a temporal resolution of vision up to 149Hz.

Our laptop indeed supports 144Hz display. In addition, we now mention the temporal resolution of pigeon vision (L480-482).

“We specifically chose a monitor with high temporal resolution to match the pigeon’s Critical Flicker Fusion Frequency (threshold at which a flickering light is perceived by the eye as steady) that reaches up to 143Hz (Dodt & Wirth, 1954).”

Lines 555-572: Did you use a control shape in your experiment? Indeed, they may escape because of a moving pattern but not a predator shape?

We did not use a control shape, as the aim of the experiment was not to directly test the effect of the shape itself. We designed the predator cue to resemble an approaching predator to ensure a response from the pigeons, but it might be that other shapes would have worked as well.

Lines 588-589: Please explain why the coordinate system of the pigeon's head is considered as the visual field?

From what I have understood, you did not reconstruct the visual fields, but only the position of the fovea. This should be noted like this as visual field involves more than a sphere around the head (binocular and monocular sectors, blind sectors, vertical extension....).

Thank you for noticing the inaccuracy, we indeed did not consider other sectors of the visual field and therefore rephrased it as (L551): “the location of the objects and conspecifics from the pigeon’s perspective”.

Lines 601-604: How much does it represent?

As this was estimated by visual inspection, we do not have the exact percentage of data loss that was caused by grooming. However, because of the number of cameras in the SMART BARN motion capture system, it is reliable in detecting markers inside the space in “ideal” conditions (without occlusion). For example, a similar set-up found marker track loss of only <1% using a model bird (Itahara & Kano 2022)

Itahara, A., & Kano, F. (2022). “Corvid Tracking Studio”: A custom-built motion capture system to track head movements of corvids. Japanese Journal of Animal Psychology, 72(1), 1–16. https://doi.org/10.2502/janip.72.1.1

Lines 610-612: You would need to cite Wood 1917 and Hodos et al. 1991 who described the presence of a fovea in this species.

We added both citations to the manuscript.

Line 611: Again, the fovea is not egal to area centralis.

Thank you, we changed it as well.

Lines 625-626: you wrote "... in a few instances....". Please explain more. How many? What proportion?

This happened in 9 observations out of 120. We now specify it in the text as well (L587-589):

“in a few instances (9 out of 120 observations), pigeons foveated on the model predator after the looming stimulus had disappeared, but these cases were excluded from our analysis.”

Lines 640-653: We missed a lot of information in the section "statistical analysis". If you moved most of the sentence from the results that describe the methods in the method section, that would be much better. Furthermore, you would need to explain more what statistics you used, which model selection, what type of data transformation....

We agree this section lacked information, and we moved the information from the result to the statistics section.

Supplmentary materials: boxplots from Fig. S1 and S2 are too small and impossible to read. Please improve the readability.

We now have enlarged these plots to make them more readable.

Public Review:

The authors used an innovative technic to study the visual vigilance based on high-acuity vision, the fovea. Combining motion-capture features and visual space around the head, the authors were able to estimate the visual fixation of free-feeding pigeon at any moment. Simulating predator attacks on screens, they showed that 1) pigeons used their fovea to inspect predators cues, 2) the behavioural state (feeding or head-up) influenced the latency to use the fovea and 3) the use of the fovea decrease the latency to escape of both the individual that foveate the predators cues but also the other flock members.

The paper is very interesting, and combines innovative technic well adapted to study the importance of high-acuity vision for spotting a predator, but also of improving the behavioural response (escaping). The results are strong and the models used are well-adapted. This paper is a major contribution to our understanding of the use of visual adaptation in a foraging context when at risk. This is also a major contribution to the understanding of individual interaction in a flock.

yess i've been waiting for this

lmao

lyanna

destorying the others later

red wedding RED WEDDING

shadow baby you will always be famous

:((

its crazy how the tullys have teld riverrun for so long when none of them are particulary strong

oh wtf

URHGRGN

HELP WHAT LMAO

ohh nvm thats yara isn't it

she's so alone :(

YESS

she's learning :(

thats crazy

Proposition:

C'était peut-être un petit laboratoire, mais il ressemble désormais davantage à une jungle en boîte. Le toit s'est effondré et des vignes gigantesques, avec leurs tiges noires et leurs feuilles violettes aussi grosses que ma tête, en ont profité pour coloniser toute la pièce; les parois en verre ont fourni la lumière nécessaire pour que les plantes envahissent tout. L'air est incroyablement humide, on a l'impression d'être dans un terrarium. Nettoyer tout l'endroit prendrait des jours

Reviewer #1 (Public Review):

Summary:

Authors explore how sex-peptide (SP) affects post-mating behaviours in adult females, such as receptivity and egg laying. This study identifies different neurons in the adult brain and the VNC that become activated by SP, largely by using an intersectional gene expression approach (split-GAL4) to narrow down the specific neurons involved. They confirm that SP binds to the well-known Sex Peptide Receptor (SPR), initiating a cascade of physiological and behavioural changes related to receptivity and egg laying.

Areas of improvement and suggestions:

(1) "These results suggest the SP targets interneurons in the brain that feed into higher processing centers from different entry points likely representing different sensory input" and "All together, these data suggest that the abdominal ganglion harbors several distinct type of neurons involved in directing PMRs"<br /> The characterization of the post-mating circuitry has been largely described by the group of Barry Dickson and other labs. I suggest ruling out a potential effect of mSP in any of the well-known post-mating neuronal circuitry, i.e: SPSN, SAG, pC1, vpoDN or OviDNs neurons. A combination of available split-Gal4 should be sufficient to prove this.

(2) Authors must show how specific is their "head" (elav/otd-flp) and "trunk" (elav/tsh) expression of mSP by showing images of the same constructs driving GFP.

(3) VT3280 is termed as a SAG driver. However, VT3280 is a SPSN specific driver (Feng et al., 2014; Jang et al., 2017; Scheunemann et al., 2019; Laturney et al., 2023). The authors should clarify this.

(4) Intersectional approaches must rule out the influence of SP on sex-peptide sensing neurons (SPSN) in the ovary by combining their constructs with SPSN-Gal80 construct. In line with this, most of their lines targets the SAG circuit (4I, J and K). Again, here they need to rule out the involvement of SPSN in their receptivity/egg laying phenotypes. Especially because "In the female genital tract, these split-Gal4 combinations show expression in genital tract neurons with innervations running along oviduct and uterine walls (Figures S3A-S3E)".

(5) The authors separate head (brain) from trunk (VNC) responses, but they don't narrow down the neural circuits involved on each response. A detailed characterization of the involved circuits especially in the case of the VNC is needed to (a) show that the intersectional approach is indeed labelling distinct subtypes and (b) how these distinct neurons influence oviposition.

Reviewer #3 (Public Review):

Summary:

This paper reports new findings regarding neuronal circuitries responsible for female post-mating responses (PMRs) in Drosophila. The PMRs are induced by sex peptide (SP) transferred from males during mating. The authors sought to identify SP target neurons using a membrane-tethered SP (mSP) and a collection of GAL4 lines, each containing a fragment derived from the regulatory regions of the SPR, fru, and dsx genes involved in PMR. They identified several lines that induced PMR upon expression of mSP. Using split-GAL4 lines, they identified distinct SP-sensing neurons in the central brain and ventral nerve cord. Analyses of pre- and post-synaptic connection using retro- and trans-Tango placed SP target neurons at the interface of sensory processing interneurons that connect to two common post-synaptic processing neuronal populations in the brain. The authors proposed that SP interferes with the processing of sensory inputs from multiple modalities.

Strengths:

Besides the main results described in the summary above, the authors discovered the following:

(1) Reduction of receptivity and induction of egg-laying are separable by restricting the expression of membrane-tethered SP (mSP): head-specific expression of mSP induces reduction of receptivity only, whereas trunk-specific expression of mSP induces oviposition only. Also, they identified a GAL4 line (SPR12) that induced egg laying but did not reduce receptivity.

(2) Expression of mSP in the genital tract sensory neurons does not induce PMR. The authors identified three GAL4 drivers (SPR3, SPR 21, and fru9), which robustly expressed mSP in genital tract sensory neurons but did not induce PMRs. Also, SPR12 does not express in genital tract neurons but induces egg laying by expressing mSP.

Weaknesses:

(1) Intersectional expression involving ppk-GAL4-DBD was negative in all GAL4AD lines (Supp. Fig.S5). As the authors mentioned, ppk neurons may not intersect with SPR, fru, dsx, and FD6 neurons in inducing PMRs by mSP. However, since there was no PMR induction and no GAL4 expression at all in any combination with GAL4-AD lines used in this study, I would like to have a positive control, where intersectional expression of mSP in ppk-GAL4-DBD and other GAL4-AD lines (e.g., ppk-GAL4-AD) would induce PMR.

(2) The results of SPR RNAi knock-down experiments are inconclusive (Figure 5). SPR RNAi cancelled the PMR in dsx ∩ fru11/12 and partially in SPR8 ∩ fru 11/12 neurons. SPR RNAi in dsx ∩ SPR8 neurons turned virgin females unreceptive; it is unclear whether SPR mediates the phenotype in SPR8 ∩ fru 11/12 and dsx ∩ SPR8 neurons.

SPR RNAi knock-down experiments may also help clarify whether mSP worked autocrine or juxtacrine to induce PMR. mSP may produce juxtacrine signaling, which is cell non-autonomous.

Reviewer #2 (Public Review):

Sex peptide (SP) transferred during mating from male to female induces various physiological responses in the receiving female. Among those, the increase in oviposition and decrease in sexual receptivity are very remarkable. Naturally, a long standing and significant question is the identity of the underlying sex peptide target neurons that express the SP receptor and are underlying these responses. Identification of these neurons will eventually lead to the identification of the underlying neuronal circuitry.

The Soller lab has addressed this important question already several years ago (Haussmann et al. 2013), using relevant GAL4-lines and membrane-tethered SP. The results already showed that the action of SP on receptivity and oviposition is mediated by different neuronal subsets and hence can be separated. The GAL4-lines used at that time were, however, broad, and the individual identity of the relevant neurons remained unclear.

In the present paper, Nallasivan and colleagues carried this analysis one step further, using new intersectional approaches and transsynaptic tracing.

Strength:

The intersectional approach is appropriate and state-of-the art. The analysis is a very comprehensive tour-de-force and experiments are carefully performed to a high standard. The authors also produced a useful new transgenic line (UAS-FRTstopFRT mSP). The finding that neurons in the brain (head) mediate the SP effect on receptivity, while neurons in the abdomen and thorax (ventral nerve cord or peripheral neurons) mediate the SP effect on oviposition, is a significant step forward in the endavour to identify the underlying neuronal networks and hence a mechanistic understanding of SP action. Though this result is not entirely unexpected, it is novel as it was not shown before.

Weakness:

Though the analysis identifies a small set of neurons underlying SP responses, it does not go the last step to individually identify at least a few of them. The last paragraph in the discussion rightfully speculates about the neurochemical identity of some of the intersection neurons (e.g. dopaminergic P1 neurons, NPF neurons). At least these suggested identities could have been confirmed by straight-forward immunostainings agains NPF or TH, for which antisera are available. Moreover, specific GAL4 lines for NPF or P1 or at least TH neurons are available which could be used to express mSP to test whether SP activation of those neurons is sufficient to trigger the SP effect.

Author response:

Reviewer #1 (Public Review):

Areas of improvement and suggestions:

(1) "These results suggest the SP targets interneurons in the brain that feed into higher processing centers from different entry points likely representing different sensory input" and "All together, these data suggest that the abdominal ganglion harbors several distinct type of neurons involved in directing PMRs"

The characterization of the post-mating circuitry has been largely described by the group of Barry Dickson and other labs. I suggest ruling out a potential effect of mSP in any of the well-known post-mating neuronal circuitry, i.e: SPSN, SAG, pC1, vpoDN or OviDNs neurons. A combination of available split-Gal4 should be sufficient to prove this.

Indeed, we have tested drivers for some of these neurons already and agree that this information is important to distinguish neurons which are direct SP target from neurons which are involved in directing reproductive behaviors.

(2) Authors must show how specific is their "head" (elav/otd-flp) and "trunk" (elav/tsh) expression of mSP by showing images of the same constructs driving GFP.

The expression pattern for tshGAL, which expresses in the trunk is already published (Soller et al., 2006). We will add images for “head” expression.

(3) VT3280 is termed as a SAG driver. However, VT3280 is a SPSN specific driver (Feng et al., 2014; Jang et al., 2017; Scheunemann et al., 2019; Laturney et al., 2023). The authors should clarify this.

According to the reviewers suggestion, we will clarify the specificity of VT3280.

(4) Intersectional approaches must rule out the influence of SP on sex-peptide sensing neurons (SPSN) in the ovary by combining their constructs with SPSN-Gal80 construct. In line with this, most of their lines targets the SAG circuit (4I, J and K). Again, here they need to rule out the involvement of SPSN in their receptivity/egg laying phenotypes. Especially because "In the female genital tract, these split-Gal4 combinations show expression in genital tract neurons with innervations running along oviduct and uterine walls (Figures S3A-S3E)".

We agree with this reviewer that we need a higher resolution of expression to only one cell type. However, this is a major task that we will continue in follow up studies.

In principal, use of GAL80 is a valid approach to restrict expression, if levels of GAL80 are higher than those of GAL4, because GAL80 binds GAL4 to inhibit its activity. Hence, if levels of GAL80 are lower, results could be difficult to interpret.

(5) The authors separate head (brain) from trunk (VNC) responses, but they don't narrow down the neural circuits involved on each response. A detailed characterization of the involved circuits especially in the case of the VNC is needed to (a) show that the intersectional approach is indeed labelling distinct subtypes and (b) how these distinct neurons influence oviposition.

Again, we agree with this reviewer that we need a higher resolution of expression to only one cell type. However, this is a major task that we will continue in follow up studies.

Reviewer #2 (Public Review):

Strength:

The intersectional approach is appropriate and state-of-the art. The analysis is a very comprehensive tour-de-force and experiments are carefully performed to a high standard. The authors also produced a useful new transgenic line (UAS-FRTstopFRT mSP). The finding that neurons in the brain (head) mediate the SP effect on receptivity, while neurons in the abdomen and thorax (ventral nerve cord or peripheral neurons) mediate the SP effect on oviposition, is a significant step forward in the endavour to identify the underlying neuronal networks and hence a mechanistic understanding of SP action. Though this result is not entirely unexpected, it is novel as it was not shown before.

We thank reviewer 2 for recognizing the advance of our work.

Weakness:

Though the analysis identifies a small set of neurons underlying SP responses, it does not go the last step to individually identify at least a few of them. The last paragraph in the discussion rightfully speculates about the neurochemical identity of some of the intersection neurons (e.g. dopaminergic P1 neurons, NPF neurons). At least these suggested identities could have been confirmed by straight-forward immunostainings agains NPF or TH, for which antisera are available. Moreover, specific GAL4 lines for NPF or P1 or at least TH neurons are available which could be used to express mSP to test whether SP activation of those neurons is sufficient to trigger the SP effect.

We appreciate this reviewers recognition of our previous work showing that receptivity and oviposition are separable. As pointed out we have now gone one step further and identified in a tour de force approach subsets of neurons in the brain and VNC.

We agree with this reviewer that we need a higher resolution of expression to only one cell type. As pointed out by this reviewer, the neurochemical identity is an excellent suggestions and will help to further restrict expression to just one type of neuron. However, this is a major task that we will continue in follow up studies.

Reviewer #3 (Public Review):

Strengths:

Besides the main results described in the summary above, the authors discovered the following:

(1) Reduction of receptivity and induction of egg-laying are separable by restricting the expression of membrane-tethered SP (mSP): head-specific expression of mSP induces reduction of receptivity only, whereas trunk-specific expression of mSP induces oviposition only. Also, they identified a GAL4 line (SPR12) that induced egg laying but did not reduce receptivity.

(2) Expression of mSP in the genital tract sensory neurons does not induce PMR. The authors identified three GAL4 drivers (SPR3, SPR 21, and fru9), which robustly expressed mSP in genital tract sensory neurons but did not induce PMRs. Also, SPR12 does not express in genital tract neurons but induces egg laying by expressing mSP.

We thank reviewer 3 for recognizing these two important points regarding the SP response that point to a revised model for how the underlying circuitry induces the post-mating response.

Weaknesses:

(1) Intersectional expression involving ppk-GAL4-DBD was negative in all GAL4AD lines (Supp. Fig.S5). As the authors mentioned, ppk neurons may not intersect with SPR, fru, dsx, and FD6 neurons in inducing PMRs by mSP. However, since there was no PMR induction and no GAL4 expression at all in any combination with GAL4-AD lines used in this study, I would like to have a positive control, where intersectional expression of mSP in ppk-GAL4-DBD and other GAL4-AD lines (e.g., ppk-GAL4-AD) would induce PMR.

We will add positive controls of for ppk-DBD expression and expand the discussion section.

(2) The results of SPR RNAi knock-down experiments are inconclusive (Figure 5). SPR RNAi cancelled the PMR in dsx ∩ fru11/12 and partially in SPR8 ∩ fru 11/12 neurons. SPR RNAi in dsx ∩ SPR8 neurons turned virgin females unreceptive; it is unclear whether SPR mediates the phenotype in SPR8 ∩ fru 11/12 and dsx ∩ SPR8 neurons.

We agree with this reviewer that the interpretation of the SPR RNAi results are complicated by the fact that SP has additional receptors (Haussmann et al 2013). The results are conclusive for all three intersections when expressing UAS mSP in SPR RNAi with respect to oviposition, e.g. egg laying is not induced in the absence of SPR. For receptivity, the results are conclusive for dsx ∩ fru11/12 and partially for SPR8 ∩ fru 11/12.

Potentially, SPR RNAi knock-down does not sufficiently reduce SPR levels to completely reduce receptivity in some intersection patterns, likely also because splitGal4 expression is less efficient.

Why SPR RNAi in dsx ∩ SPR8 neurons turned virgin females unreceptive is unclear, but we anticipate that we need a higher resolution of expression to only one cell type to resolve this unexpected result. However, this is a major task that we will continue in follow up studies.

SPR RNAi knock-down experiments may also help clarify whether mSP worked autocrine or juxtacrine to induce PMR. mSP may produce juxtacrine signaling, which is cell non-autonomous.

Whether membrane-tethered SP induces the response in a autocrine manner is an import aspect in the interpretation of the results from mSP expression.

Removing SPR by SPR RNAi and expression of mSP in the same neurons did not induce egg laying for all three intersection and did not reduce receptivity for dsx ∩ fru11/12 and for SPR8 ∩ fru 11/12. Accordingly, we can conclude that for these neurons the response is induced in an autocrine manner.

We will add this aspect to the discussion section.

Author response:

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

Reviewer #1 (Public Reviews):

Summary:

This paper by Schommartz and colleagues investigates the neural basis of memory reinstatement as a function of both how recently the memory was formed (recent, remote) and its development (children, young adults). The core question is whether memory consolidation processes as well as the specificity of memory reinstatement differ with development. A number of brain regions showed a greater activation difference for recent vs. remote memories at the long versus shorter delay specifically in adults (cerebellum, parahippocampal gyrus, LOC). A different set showed decreases in the same comparison, but only in children (precuneus, RSC). The authors also used neural pattern similarity analysis to characterize reinstatement, though I have substantive concerns about how this analysis was performed and as such will not summarize the results. Broadly, the behavioural and univariate findings are consistent with the idea that memory consolidation differs between children and adults in important ways, and takes a step towards characterizing how.

Strengths:

The topic and goals of this paper are very interesting. As the authors note, there is little work on memory consolidation over development, and as such this will be an important data point in helping us begin to understand these important differences. The sample size is great, particularly given this is an onerous, multi-day experiment; the authors are to be commended for that. The task design is also generally well controlled, for example as the authors include new recently learned pairs during each session.

Weaknesses:

As noted above, the pattern similarity analysis for both item and category-level reinstatement was performed in a way that is not interpretable given concerns about temporal autocorrelation within the scanning run. Below, I focus my review on this analytic issue, though I also outline additional concerns.

We thank the reviewer for both the positive and critical appraisal of our paper.

(1) The pattern similarity analyses were not done correctly, rendering the results uninterpretable (assuming my understanding of the authors' approach is correct).

a. First, the scene-specific reinstatement index: The authors have correlated a neural pattern during a fixation cross (delay period) with a neural pattern associated with viewing a scene as their measure of reinstatement. The main issue with this is that these events always occurred back-to-back in time. As such, the two patterns will be similar due simply to the temporal autocorrelation in the BOLD signal. Because of the issues with temporal autocorrelation within the scanning run, it is always recommended to perform such correlations only across different runs. In this case, the authors always correlated patterns extracted from the same run, which moreover have temporal lags that are perfectly confounded with their comparison of interest (i.e., from Fig 4A, the "scene-specific" comparisons will always be back-to-back, having a very short temporal lag; "set-based" comparisons will be dispersed across the run, and therefore have a much higher lag). The authors' within-run correlation approach also yields correlation values that are extremely high - much higher than would be expected if this analysis was done appropriately. The way to fix this would be to restrict the analysis to only cross-run comparisons, but I don't believe this is possible unfortunately given the authors' design; I believe the target (presumably reinstated) scene only appears once during scanning, so there is no separate neural pattern during the presentation of this picture that they can use. For these reasons, any evidence for "significant scene-specific reinstatement" and the like is completely uninterpretable and would need to be removed from the paper.

We thank the reviewer for this important input. We acknowledge that our study design leads to temporal autocorrelation in the BOLD signal when calculating RSA between fixation and scene time windows. We also recognize that we cannot interpret the significance of scene-specific reinstatement compared to zero and have accordingly removed this information. Nevertheless, our primary objective was to investigate changes in scene-specific reinstatement in relation to the different time delays of retrieval. Given that the retrieval procedure is the same over time and presumably similarly influenced by temporal autocorrelations, we argue that our results must be attributed to the relative differences in reinstatement across recent and remote trials. Bearing this in mind, we argue that our results can be interpreted in terms of delay-related changes in reinstatement. This information is discussed in pp. 21, 40 of the manuscript.

We agree with the reviewer that cross-run comparisons would be extremely interesting. This could be achieved by introducing the same items repeatedly across different runs, which was not possible in our current setup since we were interested in single exposure retrieval and practical time restriction in scanning children. We have  introduced this idea in Limitations and Discussion sections (pp. 40, 44) of the manuscript to inform future studies.

Finally, thanks to the reviewer’s comment, we identified a bug in the final steps of our RSA calculation. Fischer’s z-transformation was incorrectly applied to r-1 values, resulting in abnormally high values. We apologize for this error. We have revised the scripts and rectified the bug by correctly applying Fischer’s z-transformation to the r similarity values. We also adjusted the methods description figure accordingly (Figure 5, p. 22). This adjustment led to slightly altered reinstatement indices. Nevertheless, the overall pattern of delay-related attenuation in the scene-specific reinstatement index, observed in both children and adults, remains consistent. Similarly, we observed gist-like reinstatement uniquely in children.

b. From a theoretical standpoint, I believe the way this analysis was performed considering the fixation and the immediately following scene also means that the differences between recent and remote could have to do with either the reactivation (processes happening during the fixation, presumably) or differences in the processing of the stimulus itself (happening during the scene presentation). For example, people might be more engaged with the more novel scenes (recent) and therefore process those scenes more; such a difference would be interpreted in this analysis as having to do with reinstatement, but in fact could be just related to the differential scene processing/recognition, etc.

Thank you for your insightful comments. We acknowledge the theoretical concerns raised about distinguishing between the effects of reactivation processes occurring during fixation and differential processing of the stimulus itself during scene presentation. Specifically, the notion that engagement levels with recent scenes could result in enhanced processing, which might be misattributed to memory reinstatement mechanisms.

We argue, however, that during scene presentation, scenes are processed more “memory-wise” rather than “perception-wise”, since both recent and remote memories are well-learned, as we included only correctly recalled memories in the analysis.

We concur that scene presentations entail perceptual processing; however, such processing would be consistent across all items, given that they were presented with the same repeated learning procedure, rendering them equally familiar to participants. In addition, we would argue that distinct activation patterns elicited during varying delays are more likely attributable to memory-related processing, since participants actively engaged in a memory-based decision-making task during these intervals. We have incorporated this rationale into the discussion section of our manuscript (p. 40).

With this in mind, we hypothesized that in case of “memory-wise” processing, the neural engagement during the scene time window should be higher for remote compared to recent  items, and this increases with passing time as more control and effort should be exhibited during retrieval due to reorganized and distributed nature of memories. If the scenes are processed more “perception-wise”, we would expect higher neural engagement during the retrieval of recent compared to remote items. Our exploratory analysis (detailed overview in supplementary materials, Figure S3, Table S9) revealed a higher neural activation for remote compared to recent items in medial temporal, prefrontal, occipital and cerebellar brain regions, supporting the notion of “memory-wise” processes during scene time window. However, this exploratory analysis cannot provide a direct solution to the reviewer’s concern as our paradigm per se cannot arbitrate between “memory-wise” and “perception-wise” nature of retrieval. We added the point to the discussion (see p. 40).

c. For the category-based neural reinstatement:

(1) This suffers from the same issue of correlations being performed within the run. Again, to correct this the authors would need to restrict comparisons to only across runs (i.e., patterns from run 1 correlated with patterns for run 2 and so on). With this restriction, it may or may not be possible to perform this analysis, depending upon how the same-category scenes are distributed across runs. However, there are other issues with this analysis, as well.

(2) This analysis uses a different approach of comparing fixations to one another, rather than fixations to scenes. The authors do not motivate the reason for this switch. Please provide reasoning as to why fixation-fixation is more appropriate than fixation-scene similarity for category-level reinstatement, particularly given the opposite was used for item-level reinstatement. Even if the analyses were done properly, it would remain hard to compare them given this difference in approach.

(3) I believe the fixation cross with itself is included in the "within category" score  Is this not a single neural pattern correlated with itself, which will yield maximal similarity (pearson r=1) or minimal dissimilarity (1-pearson r=0)? Including these comparisons in the averages for the within-category score will inflate the difference between the "within-category" and "between-category" comparisons. These (e.g., forest1-forest1) should not be included in the within-category comparisons considered; rather, they should be excluded, so the fixations are always different but sometimes the comparisons are two retrievals of the same scene type (forest1-forest2), and other times different scene types (forest1-field1)

(4) It is troubling that the results from the category reinstatement metric do not seem to conceptually align with past work; for example, a lot of work has shown category-level reinstatement in adults. Here the authors do not show any category-level reinstatement in adults (yet they do in children), which generally seems extremely unexpected given past work and I would guess has to do with the operationalization of the metric.

Thank you for this important input regarding category-based reinstatement.

(1) The distribution of within-category items across runs was approximately similar and balanced. Additionally, within runs, they were presented randomly without close temporal proximity. Based on this arrangement, we believe that the issue of close temporal autocorrelation, as pointed out by the reviewer in the context of scene-specific reinstatement, may not apply to the same extent here. Again, our focus is not on the absolute level of category-based reinstatement, but the relative difference across conditions (recent vs. remote short delay vs. remote long delay) which are equally impacted by the autocorrelations.  

(2) We apologize for not motivating this analysis further. Whereas the scene-reinstatement index (i.e., fixation to scene correlation) gives us a measure of the pre-activation of a concrete scene (e.g., a yellow forest in autumn), the gist-like reinstatement gives us a measure of the pre-activation of a whole category of scenes (e.g., forests). Critically, our window of interest is the fixation period for both sets of analysis (in the absence of any significant visual input). The scene-specific reinstatement uses the scene window as a neural template against which the fixation period can be compared, while the gist-like reinstatement compares similarity of reactivation pattern for trials from the same category but differ in the exact memory content. The reinstatement of more generic, gist-like memory (e.g., forest) across multiple trials should yield more similar neural activation patterns. Significant gist-like reinstatement would suggest that neural patterns for scenes within the same category are more generic, as indicated by higher similarity among them. On the other hand, a more detailed reinstatement of specific types of forests (e.g., a yellow forest in autumn, green pine trees, a bare-leaved forest in spring, etc.) that differ in various dimensions could result in neural activation patterns that are as dissimilar as those seen in the reinstatement of scenes from entirely different categories. Through this methodology, we could distinguish between more generic, gist-like reinstatement and more specific, detailed reinstatement. This is now clarified in the manuscript, see p. 25.

(3) We apologize for the confusion caused by the figure and analysis description. In our analysis, we indeed excluded the correlation of the fixation cross with itself. Consequently, the diagonal in the figure should be blank to indicate this. This is now revised in the manuscript (Figure 7B and in Methods).

(4) We appreciate your concern and recognize that the terminology we used might not align perfectly with the conventional understanding of category-based reinstatement. Typically, category-level neural representations (as discussed in Polyn et al., 2005; Jafarpour et al., 2014; among others) are investigated to identify specific brain areas associated with encoding/perception of scenes or faces. Our aim, however, was to explore the mnemonic reinstatement of highly detailed scenes that were elaborately encoded, with the hypothesis that substantial representational transformations would occur over time and vary with age. This hypothesis is based on the memory literature, including the Fuzzy-Trace Theory, the Contextual Binding Theory, and the Trace Transformation Theory (Brainerd & Reyna, 1998; Yonelinas, 2019; Moscovitch & Gilboa, 2023). Therefore, we renamed 'category-based' reinstatement to 'gist-like' reinstatement, which clarifies our concept and better aligns it with existing literature.

We anticipated that young adults, having the ability to retain detailed narratives post-encoding, would demonstrate a reinstatement of scenes with distinct details, making these scenes dissimilar from each other (see similar findings in Sommer et al., 2021). In contrast, given the anticipated lesser strategic elaboration during learning in children, we hypothesized that they would demonstrate a shallower, more gist-like reinstatement (for instance, children recalling a forest or a field in a general sense without specific details or vivid imagery). This could result in higher category-based similarity, as children might reinstate a more generic forest concept.

We did not gather additional data on the verbal quality of reinstatement due to the limited scanning time available for children, so these assumptions remain unverified. However, anecdotal observations post-retrieval indicated that adults often reported very vivid scenes associated with clear narrative recall. In contrast, children frequently described more vague memories (e.g., “I know it was a forest”) without specific details. Future studies should include measures to assess the quality of reinstatement, potentially outside the scanning environment.

(2) I did not see any compelling statistical evidence for the claim of less robust consolidation in children.

Specifically in terms of the behavioral results of retention of the remote items at 1 vs 14 days, shown in Figure 2B, the authors conclude that memory consolidation is less robust in children (line 246). Yet they do not report statistical evidence for this point, as there was no interaction of this effect with the age group. Children had worse memory than adults overall (in terms of a main effect - i.e. across recent and remote items). If it were consolidation-specific, one would expect that the age differences are bigger for the remote items, and perhaps even most exaggerated for the 14-day-old memories. Yet this does not appear to be the case based on the data the authors report. Therefore, the behavioral differences in retention do not seem to be consolidation specific, and therefore might have more to do with differences in encoding fidelity or retrieval processes more generally across the groups. This should be considered when interpreting the findings.

Thank you for highlighting this important issue. We acknowledge that our initial description and depiction of our behavioral findings may not have effectively conveyed the main message about memory consolidation. Therefore, we have revised the behavioral results section (see pp. 12-14) to communicate our message more clearly.

As detailed in the methods section, we reported retention rates only for those items that were correctly (100%) learned on day 0, day 1, and day 14. This approach meant that different participants had varying numbers of items learned correctly. However, this strategy allowed us to address our primary question: whether memory consolidation, based on all items initially encoded successfully, is comparably robust between groups.

To illustrate the change in retention rate slopes over time for recently learned items (i.e., immediately 30 minutes after learning), short delay remote, and long delay remote items, relative to the initially correctly learned items more clearly and straightforward, we conducted the following analysis: after observing no differences between sessions in both age groups for recent items on days 1 and 14, we combined the recent items. This approach enabled us to investigate how the slope of memory retention for initially correctly learned items (with a baseline of 100%) changes over time. We observed a significant interaction between item type (recent, short delay remote, long delay remote) and group (F(3,250) = 17.35, p < .001, w2 = .16). The follow up of this interaction revealed significantly less robust memory consolidation across all delay times in children compared to young adults. This information is added in the manuscript in pp. 12-14. We have also updated the figures, incorporating the baseline of 100% correct performance.

(3) Please clarify which analyses were restricted to correct retrievals only. The univariate analyses states that correct and incorrect trials were modelled separately but does not say which were considered in the main contrast (I assume correct only?). The item specific reinstatement analysis states that only correct trials were considered, but the category-level reinstatement analysis does not say. Please include this detail.

Thank you for bringing this to our attention. We indeed limited our analysis – including univariate, specific reinstatement, and gist-like analyses – to only correctly remembered items. This decision was made because our goal was to observe delay-related changes in the neural correlates of correct memories, which are potentially stronger. We have incorporated this information into the manuscript.

(4) To what extent could performance differences be impacting the differences observed across age groups? I think (see prior comment) that the analyses were probably limited to correct trials, which is helpful, but still yields pretty big differences across groups in terms of the amount of data going into each analysis. In general, children showed more attenuated neural effects (e.g., recent/remote or session effects); could this be explained by their weaker memory? Specifically, if only correct trials are considered that means that fewer trials would be going into the analysis for kids, especially for the 14-day remote memories, and perhaps pushing the remove > recent difference for this condition towards 0. The authors might be able to address this analytically; for example, does the remote > recent difference in the univariate data at day 14 correlate with day 14 memory?

Thank you for pointing this out. Indeed, there was a significant relationship between remote > recent difference in the univariate data and memory performance at day 14 across both age group (see Figure 4C-D). The performance of all participants including children was above chance level for remote trial on day 14. In addition, although number of remote trials was lower in children (18 trials on average) in comparison to adults (22 trials on average), we believe that the number of remote trials was not too low or different across groups for the contrast.

(5) Some of the univariate results reporting is a bit strange, as they are relying upon differences between retrieval of 1- vs. 14-day memories in terms of the recent vs. report difference, and yet don't report whether the regions are differently active for recent and remote retrieval. For example, in Figure 3A, neither anterior nor posterior hippocampus seem to be differentially active for recent vs. remote memories for either age group (i.e., all data is around 0). This difference from zero or lack thereof seems important to the message - is that correct? If so, can the authors incorporate descriptions of these findings?

Thank you for this valuable input. When examining recent and remote retrieval separately, indeed both the anterior and posterior regions of the hippocampus exhibited significant activation from zero in adults (all p < .0003FDRcorr) and children (all p < .014FDRcorr, except for recent posterior hippocampus) during all delays. We include this information in the manuscript (see p. 17) and add it to the supplementary materials (Figure S2, Table S7).

(6) Please provide more details about the choices available for locations in the 3AFC task. (1) Were they different each time, or always the same? If they are always the same, could this be a motor or stimulus/response learning task? (2) Do the options in the 3AFC always come from the same area - in which case the participant is given a clue as to the gist of the location/memory? Or are they sometimes randomly scattered across the image (in which case gist memory, like at a delay, would be sufficient for picking the right option)? Please clarify these points and discuss the logic/impact of these choices on the interpretation of the results.Response: Thank you for pointing this out. During learning and retrieval, we employed the 3AFC (Three-Alternative Forced Choice) task.

The choices for locations varied across scenes while remained the same across time within individuals. There were 18 different key locations for the objects, distributed across the stimulus set. This means the locations of the objects were quite heterogeneous and differed between objects. The location of the object within the task was presented once during encoding and remained consistent throughout learning. Given the location heterogeneity, we believe our task cannot be reduced to a mere “stimulus/response learning task” but is more accurately described as an object-location associations task.

Similar to the previous description, the options for the 3AFC task did not originate from the same area, as there were 18 different areas in total. The three choice options were distributed equally: so sometimes the “correct” answer was the left option, sometimes in the middle option, or sometimes the right option. Therefore, we believe that the 3AFC task did not provide clues to the location but required detailed and precise memory of the location. Moreover, the options were not randomly scattered but rather presented close together in the scene, demanding a high level of differentiation between choices.

Taking all the above into consideration, we assert that precise object-location associative memory is necessary for a correct answer. We have added this information to the manuscript (p. 9).

(7) Often p values are provided but test statistics, effect sizes, etc. are not - please include this information. It is at times hard to tell whether the authors are reporting main effects, interactions, pairwise comparisons, etc.

Thank you for bringing this to our attention. We realize that including this information in the Tables may not be the most straightforward approach. Therefore, we have incorporated the test statistics, effect sizes, and related details into the text of the results section for clarity.

(8) There are not enough methodological details in the main paper to make sense of the results. For example, it is not clear from reading the text that there are new object-location pairs learned each day.

Thank you for pointing this out. We have added this information to the main manuscript. Additionally, we have emphasized this information in the text referring to Figure 1B.

(9) The retrieval task does not seem to require retrieval of the scene itself, and as such it would be helpful for the authors to both explain their reasoning for this task to measure reinstatement. Strictly speaking, participants could just remember the location of the object on the screen. Was it verified that children and adults were recalling the actual scene rather than just the location (e.g. via self-report)? It's possible that there may be developmental differences in the tendency to reinstate the scene depending on e.g., their strategy.

Thank you for highlighting this important point. Indeed, the retrieval task included explicit instructions for participants to recall and visualize the scene associated with the object presented during the fixation time window. Participants were also instructed to recollect the location of the object within the scene. Since the location was contextually bound to the scene and each object had a unique location in each scene, the location of the object was always embedded in the specific scene context. We have added this information to both the Methods and Results sections.

From the self-reports of the participants (which unfortunately were not systematically collected on all occasions), they indicated that when they could recall the scene and the location due to the memory of stories created during strategic encoding, it aided their memory for the scene and location immensely. We also concur with your observation that children and young adults may differ in their ability to reinstate scenes, depending on the success of their employed recall strategies. This task was conducted with an awareness of potential developmental differences in the ability to form complex contextual memories. Our elaborative learning procedure was designed to minimize these differences. It is important to note though we did not expect children to achieve performance levels fully comparable to adults. There may indeed be developmental differences in reinstatement, such as due to differences in knowledge availability and accessibility (Brod, Werkle-Bergner, & Shing, 2013). We think that these differences may underlie our findings of neural reinstatement. This is now discussed in p. 34-35, 39-43 of the manuscript.

(10) In general I found the Introduction a bit difficult to follow. Below are a few specific questions I had.

a. At points findings are presented but the broader picture or take-home point is not expressed directly. For example, lines 112-127, these findings can all be conceptualized within many theories of consolidation, and yet those overarching frameworks are not directly discussed (e.g., that memory traces go from being more reliant on the hippocampus to more on the neocortex). Making these connections directly would likely be helpful for many readers.

Thank you for bringing this to our attention. We have incorporated a summary of the general frameworks of memory consolidation into the introduction. This addition outlines how our summarized findings, particularly those related to memory consolidation for repeatedly learned information, align with these frameworks (see lines 126-138, 146-150).

b. Lines 143-153 - The comparison of the Tompary & Davachi (2017) paper with the Oedekoven et al. (2017) reads like the two analyses are directly comparable, but the authors were looking at different things. The Tompary paper is looking at organization (not reinstatement); while the Oedekoven et al. paper is measuring reinstatement (not organization). The authors should clarify how to reconcile these findings.

Thank you for highlighting this aspect. We have revised how we present the results from Tompary & Davachi (2017). This study examined memory reorganization for memories both with and without overlapping features, and it observed higher neural similarity for memories with overlapping features over time. The authors also explored item-specific reinstatement for recent and remote memories by assessing encoding-retrieval similarity. Since Oedekoven et al. (2017) utilized a similar approach, their results are comparable in terms of reinstatement. We have updated and expanded our manuscript to clarify the parallels between these studies (see lines 157-162).

c. Line 195-6: I was confused by the prediction of "stable involvement of HC over time" given the work reviewed in the Introduction that HC contribution to memory tends to decrease with consolidation. Please clarify or rephrase.

Drawing on the Contextual Binding Theory (Yonelinas et al., 2019), as well as the Multiple Trace Theory (Nadel et al., 2000) and supported for instance by evidence from Sekeres et al. (2018), we hypothesized that detailed contextual memories formed through repeated and strategic learning would strengthen the specificity of these memories, resulting in consistent hippocampal involvement for successfully recalled contextualized detailed memories. We have included additional explanatory information in the manuscript to clarify this hypothesis (see lines 217-219).

d. Lines 200-202: I was a bit confused about this prediction. Firstly, please clarify whether immediate reinstatement has been characterized in this way for kids versus adults. Secondly, don't adults retain gist more over long delays (with specific information getting lost), at least behaviourally? This prediction seems to go against that; please clarify.

Thank you for raising this important point. Indeed, there are no prior studies that examined memory reinstatement over extended durations in children. The primary existing evidence suggests that neural specificity or patterns of neural representations in children can be robustly observed, while neural selectivity or univariate activation in response to the same stimuli tends to mature later (i.e., Fandakova et al., 2019). Bearing this in mind and recognizing that such neural patterns can be observed in both children and adults, we hypothesized that adults may form stronger detailed contextual memories compared to children. By employing strategies such as creating stories, adults might more easily recall scenes without the need to resort to forming generic or gist-like memories (for example, 'a red fox was near the second left pine tree in a spring green forest'). This assumption aligns with the Fuzzy Trace Theory (Reyna & Brainerd, 1995), which posits that verbatim memories can be created without the extraction of a gist.

Conversely, we hypothesized that children, due to the ongoing maturation of associative and strategic memory components (as discussed in Shing et al., 2008 and 2010), which are dependent respectively on the hippocampus (HC) and the prefrontal cortex (PFC), would be less adept at creating, retaining, and extracting stories to aid their retrieval process. This could result in them remembering more generic integrated information, like the relationship between a fox and some generic image of a forest. We have added explanatory information to the manuscript to elucidate these points (see lines 225-230).

Reviewer #1 (Recommendations For The Authors):

(1) For Figure 3, I would highly recommend changing the aesthetics for the univariate data - at least on my screen they appear to be open boxes with solid vs. dashed lines, and as such look identical to the recent vs. remove distinction in Figure 2B. It also doesn't match the legend for me, which shows the age groups having purple vs. yellow coloring.

Thank you for this observation. We have adjusted Figure 2 (now Figure 3) (please refer to p. 14) accordingly, now utilizing purple and yellow colors to distinguish between the age groups.

(2) Lines 329-330, it is not true that "all" indices were significant from zero but this is only apparent if you read the next sentence. Please rephrase to clarify. e.g., "All ... indices with a few exceptions ... were significantly..."?

Based on the above suggestions and considering our primary focus on time-related changes in scene-specific reinstatement, we will refrain from further interpreting the relative expression of individual scene-specific indices against 0. Consequently, we have removed this information from our analysis.

(3) It is challenging to interpret some of the significance markers, such as those in Figure 3. For example what effects are being denoted by the asterisks and bars above vs. below the data on panel D? Please clarify and/or note in the legend.

We have included a note in the legend to clarify the meaning of all significance markers. In addition, we decided to state any significant main and interaction effects in the figure rather that to use significance markers.

(4) For Figures 2 and 3, only the meaning of error bars is described in the caption. It is not explained in the caption what the boxes, lines, and points denote. Please clarify.

Thank you for highlighting this. We have added explanations to the figure's annotation for clarity. Please note, that considering other review’s suggestions figure plots may have been adjusted or changed, resulting in adjustment of the explanations in the figure annotation.

(5) How were recent and remote interspersed relative to one another? The text says that each run had 10 recent and 10 remote pairs, presented in a "pseudo-random order" - not clear what that (pseudo) means in this case. Please clarify.

Thank you for raising this point. We provide this information in the Methods section “Materials and Procedure”: 'The jitters and the order of presentation for recent and remote items were determined using OptimizeXGUI (Spunt, 2016), following an exponential distribution (Dale, 1999). Ten unique recently learned pairs (from the same testing day) and ten unique remotely learned items (from Day 0) were distributed within each run (in total three runs) in the order as suggested by the software as the most optimal. There were three runs with unique sets of stimuli each resulting in thirty unique recent and thirty unique remote stimuli overall.'

(6) Figure 1A, second to last screen on the learning cycles row - what would be presented to participants here, one of these three emojis? What does the sleepy face represent? I see some of these points were mentioned in the methods, but additional clarification in the caption would be helpful.

Thank you for highlighting this. We have included this information in the figure caption. Specifically, the sleepy face symbol in the figure denotes a 'missed response'.

(7) Not clear how the jittered fixation time between object presentation and scene test is dealt with in representational similarity analyses.

Thank you for pointing this out. Beta estimates were obtained from a Least Square Separate (LSS) regression model. Each event was modeled with their respective onset and duration and, as such, one beta value was estimated per event (with the lags between events differing from trial to trial). We have edited the corresponding section (see p. 53).  

(8) It was a little bit strange to have used anterior vs posterior HPC ROIs separately in univariate analysis but then combined them for multivariate. There are many empirical and theoretical motivations for looking at item-specific and category reinstatement in anterior and posterior HPC separately, so I was surprised not to see this. Please explain this reasoning.

Thank you for pointing this out. We agree with the reviewer and included the anterior and posterior HC ROIs into the multivariate analysis. Please see the revised results section (pp. 13-15).

(9) The term "neural specificity" is introduced (line 164) without explanation; please clarify.

Thank you for bringing this to our attention. The term ‘neural specificity’ refers to the neural representational distinctiveness of information. In other words, ‘neural specificity,’ as defined by Fandakova et al. (2019), refers to the distinctiveness of neural representations in the regions that process that sensory input. We decided, however to refrain from using this term and instead to use neural representational distinctiveness, which is more self-explaining and was also introduced in the manuscript.

(10) Age range is specified as 5-7 years initially (line 187) and then 6-7 years (line 188).

We have corrected the age range in line 188 to '5 to 7 years.'

Reviewer #2 (Public Reviews):

Schommartz et al. present a manuscript characterizing neural signatures of reinstatement during cued retrieval of middle-aged children compared to adults. The authors utilize a paradigm where participants learn the spatial location of semantically related item-scene memoranda which they retrieve after short or long delays. The paradigm is especially strong as the authors include novel memoranda at each delayed time point to make comparisons across new and old learning. In brief, the authors find that children show more forgetting than adults, and adults show greater engagement of cortical networks after longer delays as well as stronger item-specific reinstatement. Interestingly, children show more category-based reinstatement, however, evidence supports that this marker may be maladaptive for retrieving episodic details. The question is extremely timely both given the boom in neurocognitive research on the neural development of memory, and the dearth of research on consolidation in this age group. Also, the results provide novel insights into why consolidation processes may be disrupted in children. Despite these strengths, there are quite a few important design and analytical choices that derail my enthusiasm for the paper. If the authors could address these concerns, this manuscript would provide a solid foundation to better understand memory consolidation in children.

We thank the reviewer for both the positive and critical appraisal of our paper.

Reviewer #2 (Recommendations For The Authors):

(1) My greatest concern is the difference in memory accuracy that emerges as soon as immediate learning, which undermines the interpretation of any consolidation-related differences. This concern is two-fold. The authors utilize an adaptive learning approach in which participants learn to criteria or stop after 4 repetitions. This type of approach leads to children seeing the stimuli more often during learning compared to adults, which on its own could have consequences for consolidation-related neural markers. Specifically, within adults theoretical and empirical work this shows that repeating information can actually lead to more gist-like representations, which is the exact profile the children are showing. While there could be a strength to this approach because it allows for equivocal memory, the decision to stop repetitions before criteria means that memory performance is significantly lower in the children, which again could have consequences to consolidation-related neural markers. First, the authors do not show any of the learning-related data which would be critical to assess the impact of this design choice. Second, there are likely differences in memory strength at the delay, making it extremely difficult to determine if the neural markers reflect development, worse memory strength, or both. This issue is compounded by the use of a 3-AFC paradigm, wherein "correct responses" included in the analysis could contain a significant amount of guessing responses. I think a partial solution to this problem is to analyze the RT data and include them in the analyses or use a drift-diffusion modeling approach to get more precise estimates of memory strength to control for this feature. An alternative is to sub-select participants in each group to have a sample matched on performance (including # of repetitions) and re-run all the analyses in this sub-sample. Without addressing these concerns it is near impossible to interpret the presented data.

Thank you for highlighting this point.

Firstly, we believe that our approach, involving strategic and repeated learning coupled with feedback, enhances the formation of detailed contextual memories. The retrieval procedure also emphasized the need for detailed memory for location. These are critical differences in experimental procedure from previous studies, which enhanced the importance of detailed representations and likely reduced the likelihood of forming gist-like memories.

Indeed, we ceased further learning after the fourth repetition. Extensive piloting, where we initially stopped after the seventh repetition, showed no improvement beyond the fourth repetition. In fact, performance tended to decline due to fatigue. Therefore, we limited the number of repetition cycles to the point where an improvement of performance was still feasible. Even though children exhibited lower final learning performance overall, we believe our procedure facilitated them to reach their maximal performance within the experimental setup.

To address the reviewer’s concern, we included learning data to illustrate the progression of learning (see Fig. 1C, pp. 9-10 in Results).

When interpreting the retention rates, it is important to note that we reported retention rates only for items that were correctly learned (100%) on day 0, day 1, and day 14. This approach meant that different participants had varying numbers of items learned correctly. However, this method enabled us to address our primary question: whether memory consolidation, based on all items initially encoded successfully, is comparably robust between the groups. To simultaneously examine the change in retention rate slopes over time for recent (30 minutes after learning), short delay (one night after) remote, and long delay (two weeks after) remote items, we conducted a separate analysis of retention rates for recent items on days 1 and 14. After observing no differences between sessions in both age groups, we combined the data for recent items. This allowed us to investigate how the slope of memory retention for initially correctly learned items (with a baseline of 100%) changes over time. We observed a significant interaction between item type (recent, short delay remote, long delay remote) and group. Analysis of this interaction revealed significantly less robust memory consolidation across all delay times for children compared to young adults. The figures have been adjusted accordingly to incorporate the baseline of 100% correct performance.

Following your suggestion, we also employed the drift diffusion model approach to characterize memory strength, calculating drift rate, boundary and non-decision time parameters. We added the results to the Supplementary Materials (section S2.1, Figure S1).

Generally, our findings indicate lower overall drift rate in children when considering all items that had to be learned. We also observed that adults show higher slope of decline in drift rate in short and long delay, which, however, are characterized still by higher memory strength compared to children. Both age groups required similar amount of evidence to make decision, which declined with delay. It may indicate an adaptation of weaker memory. Further, we observed lesser non-decision time in children compared to adults, potentially suggesting less error checking or less thorough processing and memory access through strategy in children.

Overall, these results indicate weaker memory strength in children as a quantitative measure. It may nevertheless stem from qualitatively different memory representations that children form, as our RSA findings suggest. We believe that our neural effect reflects the effect of interest (i.e., worse memory due to lower memory strength in children). When controlled for, it will take away variance of interest in the neural data. Therefore, we will refrain from including memory strength into the model. However, we will include mean RT as the indicator of general response tendencies.

Given that the paper is already very complex and long, we opted to add the diffusion model results to the Supplementary Materials (section S2.1, Fig. S1), while discussing the results in the discussion (p. 35).

(2) More discussion of the behavioral task should be included in the results, in particular the nature of the adaptive learning paradigm including the behavioral results as well as the categorical nature of the memoranda. Without this information, it is difficult for the reader to understand what category-level versus item-level reinstatement reflects.

Thank you for this valuable input. We have incorporated this information into the results section. Please refer to pp. 9-10, 12, 14, 21, 25-26 for the added details.

(3) Some of the methods for the reinstatement analysis were unclear to me or warranted further adjustment. I believe the authors compared the scene against all other scenes. I believe it would be more appropriate to only compare this against scenes drawn from the same category as opposed to all scenes. Secondly, from my reading, it seems like the reinstatement was done during the scene presentation, rather than the object presentation in which they would retrieve the scene. I believe the reinstatement results would be much stronger if it was captured during the object presentation rather than the re-presentation of the scene. Or perhaps both sets of analyses should be included.

We apologize for the confusion regarding the analysis method.

During the review process we have improved the description of this analysis and hope it is easier to follow now. In short, we used both approaches (within and between categories) to suit different goals (I.e., measuring scene-reinstatement and gist-like reinstatement).

Both types of reinstatement were assessed during the fixation cross to avoid confounds with the object itself being on the screen. We only used the scene window in one analysis (scene-reinstatement index) as a neural template to track its pre-activation during the fixation. So, as the reviewer suggests, our rationale is that the reinstatement indeed starts taking place at the short object presentation window, but importantly, extends to the fixation window. We added this clarifying information to the results section (see p. 21-27).

(4) For the univariate results, it was unclear to me when reading the results whether they were focusing on the object presentation portion of the trial or the scene presentation portion of the trial. Again, I think the claims of reinstatement related activity would be stronger if they accounted for the object presentation period.

Thank you for pointing this out. Indeed, the univariate results were based on the object presentation time window. We added this information to the results section (Fig. 3, pp. 14, 16).

(5) Further, given the univariate differences shown across age groups, the authors should re-run all analyses for the RSA controlling for mean activation within the ROI.

Thank you for highlighting this. We re-ran all analysis for the RSA controlling for the mean activation within the ROI. The results remained unchanged. We have added this information to the results section as well as in Table S8 and S11 in the Supplementary Materials for further details.

(6) The authors should include explicit tests across groups for their brain-behavior analyses if they want to make any developmentally relevant interpretations of the data. Also, It would be helpful to include similar analyses to those using the univariate signals, and not just the RSA results.

Following reviewer’s suggestion, we included brain-behavior analyses for univariate data as well as RSA data with explicit tests across groups. These can be found in the Results Section pp. 18-20, 28-32. Due to the interdependence of predefined ROIs and to avoid running a high number of correlation tests, we employed the partial least square correlation analysis for this purpose. This approach focuses on multivariate links between specified Regions of Interest (ROIs) and fluctuations in memory performance over short and long delays across different age cohorts. We argue that this multivariate strategy offers a more comprehensive understanding of the relationships between brain metrics across various ROIs and memory performance, given their mutual dependence and connectivity (refer to Genon et al. (2022) for similar discussions).

(7) There could be dramatic differences in memory processing across 5-7 year olds. I know the sample is a little small for this, but I would like to see regressions done within the middle childhood group in addition to the across-group comparisons.

We have included information detailing the relationship between memory retention rate and age within the child group (refer to p. 13). In the child group, both recent and short delay remote memory improved with age. However, the retention rate for long-delayed memory did not show a significant improvement with increasing age in children.

(8) I am concerned that the authors used global-signal as a regressor in their first-level analyses, given that there could be large changes in the amount of univariate activation that occurs across groups. This approach can lead to false positives and negatives that obscure localized differences. The authors should remove this term, and perhaps use the mean sum of the white matter or CSF to achieve the noise regressor they wanted to include.

We understand the reviewers' concerns. However, we believe that our approach is recommended for the pediatric population. Specifically, Graff et al., 2021, found that global signal regression is a highly efficacious denoising technique in their study of 4 to 8-year-old children. This technique was previously suggested for adults by Ciric et al., 2017, and the benefits in terms of motion and physiological noise removal outweigh the potential costs of removing some signal of interest, as indicated by Behzadi et al., 2007. Additionally, we incorporated the six anatomic component-based noise correction (CompCor) to account for WM and CSF signals, as recommended in the pediatric literature.

(9) The authors discuss the relationship between hippocampal reactivation and worse memory through the lens of Schapiro et al., but a new paper by Tanriverdi et al came out in JOCN recently that is more similar to the authors' findings.

Thank you for highlighting the recent paper by Tanriverdi et al. in JOCN, which aligns closely with our findings. We appreciate the suggestion and agree that exploring this alignment could further enrich our discussion on the relationship between hippocampal reactivation and memory retention. We incorporated this work in our revised manuscript .

Minor Comments

- I was surprised that the authors did not see any differences in univariate signals for memory retrieval as a function of development, as much of the prior work has shown differences (for example work by Tracy Riggins). I believe this contrast should be highlighted in the discussion.

- Given the robust differences in sleep patterns across childhood and the role of sleep in systems consolidation framework, I think this feature should be highlighted in either the introduction or discussion.

- Could the authors report on differences (or lack of differences) in head motion across the groups, and if they are different whether they could include them as a confounding variable.

I believe we included six motion parameters and their derivatives into the model

Thank you for your comments.

First, prior works on univariate signals of memory retrieval focused mostly on remembered vs forgotten contrasts, while in our study we focused on remote vs recent in short and long delay only for correctly remembered items. This can partially explain the results. We highlighted this information in the discussion session.

Second, we agree with the reviewer that sleep patterns across childhood should be addressed in the analysis. Therefore, we incorporated them in the discussion section.

Third, indeed head motion were included in the analysis as confounding variables, as adding them is highly recommended for the developmental population (e.g., Graff et al. 2021). As an example, we observed higher framewise displacement in children compared to adults, t = -16(218), p <. 001, as well as in translational y, t = -2.33(288), p = .02.

Reviewer #3 (Public Reviews):

Summary:

This study aimed to understand the neural correlates of memory recall over short (1-day) and long (14-days) intervals in children (5-7 years old) relative to young adults. The results show that children recall less than young adults and that this is accompanied by less activation (relative to young adults) in brain networks associated with memory retrieval.

Strengths:

This paper is one of few investigating long-term memory (multiple days) in a developmental population, an important gap in the field. Also, the authors apply a representational similarity analysis to understand how specific memories evolve over time. This analysis shows how the specificity of memories decreases over time in children relative to adults. This is an interesting finding.

We thank the reviewer for the appraisal of our manuscript.

Weaknesses:

Overall, these results are consistent with what we already know: recall is worse in children relative to adults (e.g., Cycowicz et al., 2001) and children activate memory retrieval networks to a lesser extent than adults (Bauer et al, 2017).

It seems that the reduced activation in memory recall networks is likely associated with less depth of memory encoding in children due to inattentiveness, reduced motivation, and documented differences in memory strategies. In regard to this, there was consideration of IQ, sex, and handedness but these were not included as covariates as they were not significant although I note p<.16 suggests there was some level of association nonetheless. Also, IQ is measured differently for the children and adults so it's not clear these can be directly contrasted. The authors suggest the instructed elaborative encoding strategy is effective for children and adults but the reference in support of this (Craik & Tulving, 1975) does not seem to support this point.

Thank you for your review, and we appreciate your valuable feedback. Here are our responses and clarifications:

Regarding the novelty of the results in terms of mentioned existent literature, we believe that in contrast to Cycowicz et al. (2001) and Bauer et al (2017), etc, we assess not only immediate memory after encoding with semantic judgement of abstract associations, but add to these findings investigating consolidation-related changes in complex associative and contextual information in much under investigated sample of 5-to-7-year-old preschoolers. With this we are able to infer also how neural representations of children change over time, providing invaluable insights into knowledge formation in this developmental cohort.

With this, the observed age differences are not so of primary importance, as time-related changes in mnemonic representations observed in children.

Regarding the assumption of inattentiveness in children, we want to emphasize that the experimenter was present throughout the learning process, closely supervising the children. We observed prompt responses to every trial in children and noted an increase in accuracy over the encoding-learning cycles, leading us to conclude that the children were indeed attentive to the task. The observed accuracy improvement across learning cycles  indicates increase in remembered information. Furthermore, we took measures to ensure their engagement, including extensive training in both verbal and computerized versions to ensure that they understood and actively created stories to support their learning.

We collected motivation data after each task execution in children, and the results indicated that they scored high in motivation. Children not only completed the tasks but also expressed their willingness to participate in subsequent appointments, highlighting their active involvement in the study.

The observed differences in the efficiency of strategy utilization were expected, given developmental differences in the associative and strategic components of memory in children, as noted in prior research (Shing, 2008, 2010).

We appreciate your point about IQ, sex, and handedness. These variables were indeed included in the behavioral models, and mean brain activation was also included in the brain data models, addressing the potential influence of these factors on our results.

While it's true that we applied different tests to measure IQ in children and adults, these tests targeted comparable subtests that addressed similar cognitive constructs. As the final IQ values are standardized, we believe it is appropriate to compare them between the two groups.

Lastly, we agree that the citation Craik & Tulving, 1975 supports the notion of effectiveness of instructed elaborative learning only in adults, but not in children. For this purpose, we added relevant literature for the child cohort (i.e., Pressley, 1982; Pressley et al., 1981; Shing et al., 2008).

Reviewer #3 (Recommendations For The Authors):

An additional point for the authors to consider is that the hypotheses were uncertain. The first is that prefrontal, parietal, cerebellar, occipital, and PHG brain regions would have greater activation over time in adults and not children - which is very imprecise as this is basically the whole brain. Moreover, brain imaging data may be in opposition to this prediction: e.g., the hippocampus has a delayed maturational pattern beyond 5-yrs (e.ge., Canada 2019; Uematsu 2012) and some cortical data predicts earlier development in these regions.

Thank you for your feedback, and we appreciate your insights regarding our hypotheses.

The selection of our regions of interest (ROIs) was guided by prior literature that has demonstrated the interactive involvement of multiple brain areas in memory retrieval and consolidation processes. Additionally, our recent work utilizing multivariate partial least square correlation analysis (Schommartz, 2022, Developmental Cognitive Neuroscience) has indicated that unique profiles derived from the structural integrity of multiple brain regions are differentially related to short and long-delay memory consolidation.

Indeed, the literature suggests that the hippocampus may exhibit a more delayed maturational pattern extending into adolescence, as supported by studies such as Canada (2019) and Uematsu (2012), etc. We added this information as well as findings from the literature on cortical development to be more balanced in our review of the literature.

Given this complexity, we believe it is important to emphasize in our discussion that both the medial temporal lobe, including the hippocampus, and cortical structures, as well as the cerebellum, undergo profound neural maturation. We highlight these nuances in our revised manuscript to provide a more comprehensive perspective on the developmental differences in memory retention over time.

The writing was challenging to follow - consider as an example on page 9 the sentence that spans 10 lines of text.

Thank you for bringing this to our attention. We have carefully reviewed the manuscript and have made efforts to streamline the text, ensuring that sentences are not overly long or complex to improve readability and comprehension.

I found the analysis (and accompanying figures) a bit of a data mine - there are so many results that are hard to digest and in other cases highly redundant one from the other. This may be resolved in part by moving redundant findings to the supplemental. Some were hard to follow - so when there is a line between recent and recent data, that seems confusing to connect data that, I believe, are different sets of items. Later scatterplots (Fig 7) have pale yellow dots that I had a hard time seeing.

Thank you for bringing up your concerns regarding the analysis and figures in our manuscript. We have carefully considered your feedback and made several improvements to address these issues.

To alleviate the challenge of digesting numerous results, we have taken steps to enhance clarity and reduce redundancy. Specifically, we have moved some of the redundant findings to the supplementary sections, which should help streamline the main manuscript and make it more reader friendly.

Regarding the line between 'recent' and 'recent data,' figure were transformed to a clearer version. Furthermore, we have improved the visibility of certain elements, such as the pale-yellow dots in the scatterplots (Fig 1, 2, 4, etc. ), to ensure that readers can better discern the data points.

This is a tricky topic to wrap my head around because as they are stating that our thoughts that we constantly isn't matter or energy. I believe that they are stating that the y usually have to use experiments based on observation but to what extent does that limit the results of an experiment?

But your reality unfortunately looks very different.

You're too much in your head...

Human's as judge of relative performance of two LLMs, scores become reward signal.

Author response:

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

Reviewer #1 (Public Review):

I'll begin by summarizing what I understand from the results presented, and where relevant how my understanding seems to differ from the authors' claims. I'll then make specific comments with respect to points raised in my previous review (below), using the same numbering. Because this is a revision I'll try to restrict comments here to the changes made, which provide some clarification, but leave many issues incompletely addressed.

As I understand it the main new result here is that certain recurrent network architectures promote emergence of coordinated grid firing patterns in a model previously introduced by Kropff and Treves (Hippocampus, 2008). The previous work very nicely showed that single neurons that receive stable spatial input could 'learn' to generate grid representations by combining a plasticity rule with firing rate adaptation. The previous study also showed that when multiple neurons were synaptically connected their grid representations could develop a shared orientation, although with the recurrent connectivity previously used this substantially reduced the grid scores of many of the neurons. The advance here is to show that if the initial recurrent connectivity is consistent with that of a line attractor then the network does a much better job of establishing grid firing patterns with shared orientation.

Beyond this point, things become potentially confusing. As I understand it now, the important influence of the recurrent dynamics is in establishing the shared orientation and not in its online generation. This is clear from Figure S3, but not from an initial read of the abstract or main text. This result is consistent with Kropff and Treves' initial suggestion that 'a strong collateral connection... from neuron A to neuron B... favors the two neurons to have close-by fields... Summing all possible contributions would result in a field for neuron B that is a ring around the field of neuron A.' This should be the case for the recurrent connections now considered, but the evidence provided doesn't convincingly show that attractor dynamics of the circuit are a necessary condition for this to arise. My general suggestion for the authors is to remove these kind of claims and to keep their interpretations more closely aligned with what the results show.

We would like to clarify that the simple (flexible) attractor is a weaker condition than the ones previously used to align grid cells. However, by no means we claim that it is a necessary condition for grid maps to align. Other architectures, certainly more complex ones but perhaps even simpler ones, can align grid maps in our model.

Major (numbered according to previous review)

(1) Does the network maintain attractor dynamics after training? Results now show that 'in a trained network without feedforward Hebbian learning the removal of recurrent collaterals results in a slight increase in gridness and spacing'. This clearly implies that the recurrent collaterals are not required for online generation of the grid patterns. This point needs to be abundantly clear in the abstract and main text so the reader can appreciate that the recurrent dynamics are important specifically during learning.

We respectfully disagree with the interpretation of this result. In this model cells self-organize to produce aligned grid maps. In such systems it makes sense to characterize the equilibrium states of the system. We turned learning off in Figure S3 to show that the recurrent connections have a contractive effect on grid spacing. But artificially turning off learning means that one can no longer make claims about the equilibrium states of the system, since it can no longer evolve freely. In a functional network, if the recurrent attractor is removed, the system will evolve towards poor gridness and no alignment no matter what the starting point is, as also shown in Figure S3. Several experimental results invite us to think of grid cells as the equilibrium solution of a series of constraints that is ready to change at any time: Barry et al, 2012; Yoon et al, 2013; Carpenter et al, 2015; Krupic et al, 2015; Krupic et al, 2018; Jayakumar et al, 2019.

One point in which we perhaps agree with the reviewer is that information about the hexagonal maps is kept in the feedforward weights, while behavior and the recurrent collaterals act as constraints of which these feedforward weights are the equilibrium solution.

(2) Additional controls for Figure 2 to test that it is connectivity rather than attractor dynamics (e.g. drawing weights from Gaussian or exponential distributions). The authors provide one additional control based on shuffling weights. However, this is far from exhaustive and it seems difficult on this basis to conclude that it is specifically the attractor dynamics that drive the emergence of coordinated grid firing.

Again, we do not claim that this is the only way in which grid maps can be aligned, but it is the simplest one proposed so far. We were asked if it was the specific combination of input weights to a cell rather than the organization provided by the attractor which resulted in aligned maps. By shuffling the inputs to a cell we keep the combination of inputs invariant but lose the attractor architecture. Since grid maps in this new situation are not aligned, we can safely conclude that it is not the combination of inputs per se, but the specific organization of these inputs that allows grid alignment. It is not fully clear to us what ‘exhaustive’ means in this context.

(3) What happens if recurrent connections are turned off? The new data clearly show that the recurrent connections are not required for online grid firing, but this is not clear from the abstract and is hard to appreciate from the main text.

This point is related to (1). Absent this constraint, Figure S3 shows that the system evolves toward larger spacing, with poorer gridness and no alignment.

(4) This is addressed, although the legend to Fig. S2D could provide an explanation / definition for the y-axis values.

We have now added: Mean input fields are the sum of all inputs of a given kind entering a neuron at a given moment in time, averaged across cells and time.

(5) Given the 2D structure of the network input it perhaps isn't surprising that the network generates 2D representations and this may have little to do with its 1D connectivity. The finding that the networks maintain coordinated grids when recurrent connections are switched off supports my initial concern and the authors explanation, to me at least, remain confusing. I think it would be helpful to consider that the connectivity is specifically important for establishing the coordinated grid firing, but that the online network does not require attractor dynamics to generate coordinated grid firing.

This point is related to (1) and (3). We agree with the reviewer that the input lies within a 2D manifold, but this is not something that the network has to find out because it receives one datapoint of information at a time. This alone is not enough to form aligned grid cells, since each grid cell can find a roughly equivalent equilibrium in a different direction. It is only the constraint imposed by the recurrent collaterals that aligns grid maps, and, as we show, this constraint does not need to be constructed ad hoc to work on 2D, as previously thought. When recurrent connections are switched off, the system evolves toward unaligned grid maps, with larger spacing and lower gridness. Regarding the results obtained after modifying the network and turning off learning, we think they have a very limited scope (in this case showing the contractive effect of recurrent collaterals on grid spacing), given that the system is artificially being kept out of its natural equilibrium.

(6) Clarity of the introduction. This is somewhat clearer, but I wonder if it would be hard for someone not familiar with the literature to accurately appreciate the key points.

We have made our best effort to improve the clarity of the introduction.

(7) Remapping. I'm not sure why this is ill posed. It seems the proposed model can not account for remapping results (e.g. Fyhn et al. 2007). Perhaps the authors could just clearly state this as a limitation of the model (or show that it can do this).

We view our model as perfectly consistent with Fyhn et al, 2007. Remapping is not triggered by the network itself, though, but rather by a re-arrangement of the inputs requiring the network to learn new associations. Different simulations of the same model with identical parameters can be interpreted as remapping experiments.

Reviewer #3 (Public Review):

Summary:

The paper proposes an alternative to the attractor hypothesis, as an explanation for the fact that grid cell population activity patterns (within a module) span a toroidal manifold. The proposal is based on a class of models that were extensively studied in the past, in which grid cells are driven by synaptic inputs from place cells in the hippocampus. The synapses are updated according to a Hebbian plasticity rule. Combined with an adaptation mechanism, this leads to patterning of the inputs from place cells to grid cells such that the spatial activity patterns are organized as an array of localized firing fields with hexagonal order. I refer to these models below as feedforward models.

It has already been shown by Si, Kropff, and Treves in 2012 that recurrent connections between grid cells can lead to alignment of their spatial response patterns. This idea was revisited by Urdapilleta, Si, and Treves in 2017. Thus, it should already be clear that in such models, the population activity pattern spans a manifold with toroidal topology. The main new contributions in the present paper are (i) in considering a form of recurrent connectivity that was not directly addressed before. (ii) in applying topological analysis to simulations of the model. (iii) in interpreting the results as a potential explanation for the observations of Gardner et al.

We wanted to note that we do not see this paper as proposing an alternative to the attractor hypothesis, given that we use attractor networks, but rather as an exploration of possibilities not yet visited by this hypothesis.

Strengths:

The exploration of learning in a feedforward model, when recurrent connectivity in the grid cell layer is structured in a ring topology, is interesting. The insight that this not only align the grid cells in a common direction but also creates a correspondence between their intrinsic coordinate (in terms of the ring-like recurrent connectivity) and their tuning on the torus is interesting as well, and the paper as a whole may influence future theoretical thinking on the mechanisms giving rise to the properties of grid cells.

Weaknesses:

(1) In Si, Kropff and Treves (2012) recurrent connectivity was dependent on the head direction tuning, in addition to the location on a 2d plane, and therefore involved a ring structure. Urdapilleta, Si, and Treves considered connectivity that depends on the distance on a 2d plane. The novelty here is that the initial connectivity is structured uniquely according to latent coordinates residing on a ring.

The recurrent architectures in the cited works are complex and require arranging cells in a 2D manifold to calculate connectivity based on their relative 2D position. In other words, the 2D structure is imprinted in the architecture, as in our 2D condition. In this work the network is much simpler and only requires neighboring relations in 1D. Such relationships have been shown to spontaneously emerge in the hippocampal formation (Pastalkova et al, 2008; Gonzalo Cogno et al, 2024).

(2) The paper refers to the initial connectivity within the grid cell layer as one that produces an attractor. However, it is not shown that this connectivity, on its own, indeed sustains persistent attractor states. Furthermore, it is not clear whether this is even necessary to obtain the results of the model. It seems possible that (possibly weaker) connections with ring topology, that do not produce attractor dynamics but induce correlations between neurons with similar locations on the ring would be sufficient to align the spatial response patterns during the learning of feedforward weights.

Regarding the first part of the comment, the recurrent collaterals create one or at times multiple bumps of activity in the network so that neighboring (interconnected) cells activate together. An initial random state of activity rapidly falls into this dynamic, constrained by the attractor. To us this is not surprising given that this connectivity is the classical means of creating a continuous attractor. Perhaps there is some deeper meaning in this comment that we are not fully grasping.

Regarding the second part of the comment, we fully agree with the reviewer. We are presenting what so far is the simplest connectivity that can align grid maps, but by no means we claim that it is the simplest possible one. Regarding weaker connections with ring topology, we show in Figure S2 that a ring attractor with too weak or too strong connections is incapable of aligning grids, since a balance between feedforward and feedback inputs is required.

(3) Given that all the grid cells are driven by an input from place cells that span a 2d manifold, and that the activity in the grid cell network settles on a steady state which is uniquely determined by the inputs, it is expected that the manifold of activity states in the grid cell layer, corresponding to inputs that locally span a 2d surface, would also locally span a 2d plane. The result is not surprising. My understanding is that this result is derived as a prerequisite for the topological analysis, and it is therefore quite technical.

We understand that the reviewer is referring to the motivation behind studying local dimensionality. We agree that the topological analysis approach is quite technical, but it provides unique insights. The theorem of closed surfaces, which allows us to deduce a toroidal topology from Betti numbers (1,2,1), only applies to closed surfaces. One thus needs to show that the point cloud is a surface (local dimensionality of 2) and is closed (no borders or singularities). If borders or singularities were present, a toroidal topology could not be claimed from these Betti numbers. Thus, it is a crucial step of the analysis.

(4) The modeling is all done in planar 2d environments, where the feedforward learning mechanism promotes the emergence of a hexagonal pattern in the single neuron tuning curve. Under the scenario in which grid cell responses are aligned (i.e. all neurons develop spatial patterns with the same spacing and orientation) it is already quite clear, even without any topological analysis that the emerging topology of the population activity is a torus.

However, the toroidal topology of grid cells in reality has been observed by Gardner et al also in the wagon wheel environment, in sleep, and close to boundaries (whereas here the analysis is restricted to the a sub-region of the environment, far away from the walls). There is substantial evidence based on pairwise correlations that it persists also in various other situations, in which the spatial response pattern is not a hexagonal firing pattern. It is not clear that the mechanism proposed in the present paper would generate toroidal topology of the population activity in more complex environments. In fact, it seems likely that it will not do so, and this is not explored in the manuscript.

We agree that our work was constrained to exploration in 2D and that the situations posed by the reviewer are challenging, but we do not see them as unsurmountable. The wagon wheel shows a preservation of toroidal topology locally, where the behavior of the animal is rather 2-dimensional. Globally, hexagonal maps are lost, which is compatible with some flexibility in the way grid maps are formed. If sleep meant that all inputs are turned off, our model would predict a dynamic dictated by the architecture (1D for the ring attractor, for example), but we do not really know that this is the case. In the future, we intend to explore predictive activity along the linear attractor, which could both result in path integration and in some level of preservation of the activity when inputs are completely turned off.

Regarding boundaries, as we have argued before, the cited work chooses to filter away what looks like more than half of the overall explained variance through PCA, and this is only before applying a non-linear dimensionality reduction algorithm. It is specifically shown that the analyzed components are the ones with global periodicity throughout the environment. Thus, it is conceivable that through this approach, local irregularities found only at the borders are disregarded in favor of a clearer global picture. While using a different methodology, our approach follows a similar spirit, albeit with far less noisy data.

(5) Moreover, the recent work of Gardner et al. demonstrated much more than the preservation of the topology in the different environments and in sleep: the toroidal tuning curves of individual neurons remained the same in different environments. Previous works, that analyzed pairwise correlations under hippocampal inactivation and various other manipulations, also pointed towards the same conclusion. Thus, the same population activity patterns are expressed in many different conditions. In the present model, this preservation across environments is not expected. Moreover, the results of Figure 6 suggest that even across distinct rectangular environments, toroidal tuning curves will not be preserved, because there are multiple possible arrangements of the phases on the torus which emerge in different simulations.

We agree with this observation. A symmetry in our implementation results in the fact that only ~50% of times the system falls in the preferred solution, and the rest of the times it falls into other local minima. Whether this result is at odds with current observations can be debated on the basis of probabilities. However, we believe that the symmetry we found is purely circumstantial, and that it can be broken by elements such as head direction modulation or other ingredients used to achieve path integration. In other words, we acknowledge that symmetry is an issue of the implementation we show here (which has been kept as simple as possible to serve as a proof-of-principle) but we do not think that it is a defining feature of flexible attractors in general. We expect that future implementations that incorporate path integration capabilities will not present this kind of symmetry in the space of solutions.

Regarding the rigid phase translation across modalities, while this effect is very clear in Gardner et al, it is less so in other datasets. The analyses shown in Hermansen et al (2024) can rather be interpreted as somewhere in the way between perfect rigid translation and fully randomized phases across navigation modalities.

(6) In real grid cells, there is a dense and fairly uniform representation of all phases (see the toroidal tuning of grid cells measured by Gardner et al). Thus, the highly clustered phases obtained in the model (Fig. S1) seem incompatible with the experimental reality. I suspect that this may be related to the difficulty in identifying the topology of a torus in persistent homology analysis based on the transpose of the matrix M.

We partly agree with this observation and note that a pattern of ordered phases is an issue not only for the 1D attractor but also for the 2D one, which appears much more uniform than in experimental data. The low number of neurons we used for computational economy and the full connectivity could be key ingredients to generate these phase patterns. To show that this is not a defining feature of flexible attractors, apart from the fact that these patterns appear also with non-flexible 2D architectures, we included in Figure S1 simulations with ‘fragmented 1D’ architectures. In this case the architecture is a superposition of 20 random 1D stripe-like attractors. While the alignment of maps achieved with this architecture is almost at the same level as the one obtained with 1D and 2D attractors, the phases are much more similar to what has been observed experimentally, and less uniform than what is obtained with 2D attractors.

(7) The motivations stated in the introduction came across to me as weak. As now acknolwledged in the manuscript, attractor models can be fully compatible with distortions of the hexagonal spatial response patterns - they become incompatible with this spatial distortions only if one adopts a highly naive and implausible hypothesis that the attractor state is updated only by path integration. While attractor models are compatible with distortions of the spatial response pattern, it is very difficult to explain why the population activity patterns are tightly preserved across multiple conditions without a rigid two-dimentional attractor structure. This strong prediction of attractor models withstood many experimental tests - in fact, I am not aware of any data set where substantial distortions of the toroidal activity manifold were observed, despite many attempts to challenge the model. This is the main motivation for attractor models. The present model does not explain these features, yet it also does not directly offer an explanation for distortions in the spatial response pattern.

Some interesting examples are experiments in 3D, where grid cells presumably communicate with each other through the same recurrent collaterals, but global periodicity is lost and only some local order is preserved even away from boundaries (Ginosar et al, 2021; Grieves et al, 2021). While these datasets have not been explored using topological analysis, they serve as strong motivators to understanding 2D grid cells as one equilibrium solution that arises under some set of constraints, but belongs to a wider space of possible solutions that may arise as well under more flexible constraints. Even (and especially) if one adheres to the hypothesis that grid cells are pre-wired into a 2D torus, a concept like flexible attractors might become useful to understand how their activity is rendered in 3D. Another strong motivation is our lack of understanding of how a perfectly balanced 2D structure is formed and maintained. Simpler architectures could be thought of as alternatives, but also as an intermediate step towards it.

Regarding the rigid phase translation across modalities, while this effect is very clear in Gardner et al, it is less so in other datasets. The analyses shown in Hermansen et al (2024) can rather be interpreted as somewhere in the way between perfect rigid translation and fully randomized phases.

In a separate point, although it might not be strictly related to the comment, we do not fully share the idea that persistent activity patterns during sleep are necessary or sufficient conditions for attractor dynamics, although we do agree that attractors could be the mechanism behind them and any alternative is at least as complex as attractors. On the necessity side, attractors in the hippocampus are not constantly engaged (Wills et al, 2005). For sufficiency, one should prove that no other network is capable of reproducing the phenomenon, and to our best knowledge we are still far from that point.

(8) There is also some weakness in the mathematical description of the dynamics. Mathematical equations are formulated in discrete time steps, without a clear interpretation in terms of biophysically relevant time scales. It appears that there are no terms in the dynamics associated with an intrinsic time scale of the neurons or the synapses (a leak time constant and/or synaptic time constants). I generally favor simple models without lots of complexity, yet within this style of modelling, the formulation adopted in this manuscript is unconventional, introducing a difficulty in interpreting synaptic weights as being weak or strong, and a difficulty in interpreting the model in the context of other studies.

We chose to keep the model as simple as possible and in the line of previous publications developing it. However, we see the usefulness of putting it in what in the meantime has become a canonical framework. Fortunately this has been done by D’Albis and Kempter (2017). In our simplified version of the model there is no leak term and adaptation on its own brings down activity in the absence of input, but we agree that such a term could be added, albeit not without modifying all other network parameters.

In my view, the weaknesses discussed above limit the ability of the model, as it stands, to offer a compelling explanation for the toroidal topology of grid cell population activity patterns, and especially the rigidity of the manifold across environments and behavioral states. Still, the work offers an interesting way of thinking on how the toroidal topology might emerge.

Reviewer 1:

Reviewer #1 (Recommendations For The Authors):

See comments above. In addition:

(1) Abstract: '...interconnected by a two-dimensional attractor guided by path integration'. This is unclear. I think the intended meaning might be along the lines of '...their being computed by a 2D continous attractor that performs path integration'?

'path integration allowing for no deviations from the hexagonal pattern' This is incorrect. Local modulation of the gain of the speed input to a standard CAN would distort the grid pattern.

'Using topological data analysis, we show that the resulting population activity is a sample of a torus' Activity in the model?

'More generally, our results represent a proof of principle against the intuition that the architecture and the representation manifold of an attractor are topological objects of the same dimensionality, with implications to the study of attractor networks across the brain' I guess one might hold this intuition, but it strikes me as obvious that if you impose an sufficiently strong n-dimensional input on a network then it it's activity could have the same dimensionality. I don't really see this as being a point worth highlighting. Perhaps the more interesting point, it that during learning the recurrent connectivity aligns the grid fields of neurons in the network, and this may be a specific function of the 1D attractor dynamcis, although I don't think the authors have made this point convincing.

'The flexibility of this low dimensional attractor allows it to negotiate the geometry of the representation manifold with the feedforward inputs'. See above for comments on the use of 'negotiate'.

'while the ensemble of maps preserves features of the network architecture'. I don't understand this. What is the 'ensemble of maps' and what are the features referred to.

We have reviewed the abstract considering these points. Regarding the ‘strong n-dimensional input’, we want to point out that it is not the input itself that generates a torus (the no attractor condition does not lead to a torus) but rather the interplay between the input and the attractor.

‘Perhaps the more interesting point …’, we do not fully understand how this sentence deviates from our own conclusions. We here show that a strong n-dimensional input is not enough to align grid cells (produce a n-torus), it is the interplay between inputs and attractor dynamics that does so, even if the attractor is not n-dimensional in terms of architecture.

The ensemble of maps refers to the transpose of the population activity matrix, where each point in the cloud is a map, and the features refer to the persistent homology.

(2) The manuscript still fails to clarify the difference between a model that path integrates in two dimensions and a model that simply represents information with a given dimensionality. The argument that it's surprising that a network with 1D architecture represents a higher dimensional input strikes me as incorrect and an unnecessary attempt to argue for conceptual importance. At least to me this isn't surprising. It would be surprising if the 1D network could path integrate but this doesn't seem to be the case.

In response to the reviewer’s concerns, we have made clear in the introduction and discussion that this model has no path integration capabilities, although we aim to develop a model capable of path integration using the kind of simple architecture presented here. We want to highlight here that equating attractor dynamics with path integration would be a conceptual mistake.

(3) Other wording also seems to make unnecessary conceptual claims. E.g. The repeated use of 'negotiate' implies some degree of intelligence, or at least an exchange of information, that isn't shown to exist. I wonder if more precise language could be used? As I understand it the dimensionality is bounded by the inputs on the one hand, and the network connectivity on the other, with the actual dimensionality being a function of the recurrent and feedforward synaptic weights. There's clearly some role for the relative weights and the properties of plasticity rules, but I don't see any evidence for a negotiation.

An interesting observation in Figure S2 is that grid maps are aligned only if the relative strength of feedforward and recurrent inputs is similar. If one of them can impose over the other, grid maps do not align. This equilibrium can metaphorically be thought of as a negotiation instance, where the negotiation is an emergent property of the system rather than something happening at an individual synapse.

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

Reviewer #1:

Reviewer #1 (Recommendations For The Authors):

Major

(1) What is the evidence that, after training, the 1D network maintains its attractor dynamics when feedforward inputs are active? If the claim is that it does then it's important to provide evidence, e.g. responses to perturbations, or other tests. The alternative is that after training the recurrent inputs are drowned out by the feed forward spatial inputs.

We agree with the reviewer on the importance of this point. In our model, networks are always learning, and the population activity represented by aligned grid maps in a trained network is a dynamic equilibrium that emerges from the interplay between feedforward and collateral constraints. If Hebbian learning is turned off, one gets a snapshot of the network at that moment. We now show in Fig. S3 that in a trained network without feedforward Hebbian learning the removal of recurrent collaterals results in a slight increase in gridness and spacing. The expansion is due to the fact that, as we argue in the Results section, the attractor has a contractive effect on grid maps, which could relate to observations in novel environments (Barry et al, 2007). If Hebbian learning is turned on in the same situation, the maps, no longer constrained by the attractor, drift toward the equilibrium solution of the ‘No attractor’ condition, with significantly larger spacing, no alignment and lower individual gridness. Thus, the attractor is the force preventing them to do so when feedforward Hebbian learning is on.

These observations point to the key role played by the attractor not only in forming but also in sustaining grid activity. The dynamic equilibrium framework fits well known properties of the system, such as its capacity to recalibrate very fast (Jayakumar et al, 2019), although this particular feature cannot be modeled with the current version of our model, that lacks path integration capabilities.

(2) It would be useful to include additional control conditions for Figure 2 to test the hypothesis that it is simply connectivity, rather than attractor dynamics, that drives alignment.

This could be achieved by randomly assigning strengths to the recurrent connections, e.g. drawing from exponential or Gaussian distributions.

We agree and have included Fig. S2b-d, showing that the same distribution of collateral input weights entering each neuron, but lacking the 1D structure provided by the attractor, does not align grid maps. This is achieved by shuffling rows in the connectivity matrix, while avoiding self connections to make the comparison fair (self connections substantially alter the dynamic of the network, making it much more rigid). We observed that individual grid maps have very low gridness levels, even lower than in the no-attractor condition. In contrast, they have levels of population gridness slightly higher than in the no-attractor condition, but closer to 0 than to levels achieved with attractors. Our interpretation of these results is that irregular connectivity achieves some alignment in a few arbitrary directions and/or locations, which improves the coordination between maps at the expense of impairing rather than improving hexagonal responses of individual cells. Such observations stand in clear context to what is observed with continuous attractors with an orderly architecture.

These results suggest that it is the structure of the attractor that allows grid cells to be aligned rather than the mere presence of recurrent collateral connections.

(3) It seems conceivable that once trained the recurrent connections would no longer be required for alignment. Can this be evaluated by considering what happens if the recurrent connections are turned off after training (or slowly turned off during training)? Does the network continue to generate aligned grid fields?

This point has elements in common with point 1. As we argued in that response, the attractor has two main effects on grid maps: it aligns them and it contracts them. If the attractor is turned off, feedforward Hebbian learning progressively drives maps toward the solution obtained for the ‘no attractor’ condition, characterized by maps with larger spacing, poorer gridness and lack of alignment.

(4) After training what is the relative strength of the recurrent and feedforward inputs to each neuron?

Both recurrent and feedforward synaptic-strength matrices are normalized throughout training, so that the overall incoming synaptic strength to each neuron is invariant. Because of this, although individual feed-forward and recurrent input fields vary dynamically, their average is constant, with the exception of the very first instances of the simulation, before a stable regime is reached in grid-cell activity levels. We have included Fig. S2d, showing the dynamics of feedforward and recurrent mean fields throughout learning as well as their ratio. In addition, Fig. S2a shows that the strength of recurrent relative to feedforward inputs is an important parameter, since alignment is only obtained in an intermediate range of ratios.

(5) It would be helpful to also evaluate the low dimensional structure of the input to the network. Assuming it has a 2D structure, as it represents 2D space, can an explanation be provided for why it is surprising that the trained network also encodes activity with a 2D manifold? It strikes me that the more interesting finding might relate to alignment of the grids rather than claims about a 1D attractor encoding a 2D representation. Either way, stronger evidence and clearer discussion would be helpful.

The reviewer is correct in assuming that the input has a 2D structure, that can be represented by a sheet embedded in a high dimensional space and thus has the Betti numbers [1,0,0]. The surprising element in our results is that we are showing for the first time that the population activity of an attractor network is constrained to a manifold that results from the negotiation between the architecture of the attractor and the inputs, and does not merely reflect the former as previously assumed. In this sense, the alignment of grid cells by a 1D attractor is an instance of the more general case that 1D attractors can encode 2D representations.

It is certainly the case that the 2D input is a strong constraint pushing population activity toward a 2D manifold. However, the final form of the 2D manifold is strongly constrained by the attractor, as shown by the contrast with the no-attractor condition (a 2D sheet, as in the input, vs a torus when the attractor is present). The 1D attractor is able to flexibly adapt to the constraint posed by the inputs while doing its job (as demonstrated in previous points), which results in 2D grid maps aligned by a 1D attractor. Generally speaking, this work provides a proof of principle demonstrating that the topology of the attractor architecture and the manifold of the population activity space need not be identical, as previously widely assumed by the attractor community, and need not even have the same dimensionality. Instead, a single architecture can potentially be applied to many purposes. Hence, our work provides a valuable new perspective that applies to the study of attractors throughout the brain.

(6) The introduction should be clearer about the different types of grid model and the computations they implement. E.g. The authors' previous model generates grid fields from spatial inputs, but if my understanding is correct it isn't able to path integrate. By contrast, while the many 2D models with continuous attractor dynamics also generate grid representations, they do so by path integration mechanisms that are computationally distinct from the spatial transformation implemented by feedforward models (see also general comments above).

We agree with the reviewer and have made this point explicit in the introduction.

(7) A prediction from continuous attractor models is that when place cells remap the low dimensional manifold of the grid activity is unaffected, except that the location of the activity bump is moved. It strikes me as important to test whether this is the case for the model presented here (my intuition is that it won't be, but it would be important to establish either way).

We want to emphasize that our model is a continuous attractor model, so the question regarding the difference between what our model and continuous attractor network models predict is an ill-posed one. One of our main conclusions is precisely that attractors can work in a wider spectrum of ways than previously thought.

In lack of a better definition, our multiple simulations could be thought of as training in different arenas. It is true that in our model maps take time to form, but this is also the case in novel environments (Barry et al, 2007 ), and continuous attractor models exclusively or strongly guided by self motion cues struggle to replicate this phenomenon. We show that the current version of our model accepts multiple solutions (in practice four but conceptually infinite countable), all of them resulting in a torus for the population activity (i.e. the same topology or low dimensional manifold). It is not clear to us how easy it would be to differentiate between most of these solutions in experimental data, with only incomplete information. This said, incorporating a symmetry-breaking ingredient to the model, for example related to head direction modulation, could perhaps lead to the prevalence of a single type of solution. We intend to explore this possibility in the future in order to add path-integration capabilities to the system, as described in the discussion.

(8) The Discussion implies that 1D networks could perform path integration in a manner similar to 2D networks. This is a strong claim but isn't supported by evidence in the study. I suggest either providing evidence that this is the case for models of this kind or replacing it with a more careful discussion of the issue.

The current version of our model has no path integration capabilities, as is now made explicit in the Introduction and Discussion. In addition, we have now made clear that the idea that path integration could perhaps be implemented using 1D networks is, although reasonable, purely speculative.

Minor

(1) Introduction. 'direct excitatory communication between them'. Suggest rewording to 'local synaptic interactions', as communication can also be purely inhibitory (e.g. Burak and Fiete, 2009) or indirect by excitation of local interneurons (e.g. Pastoll et al., Neuron, 2013).

We agree and have adopted this phrasing.

(2) The decision to focus the topology analysis on the 60 cm wide central square appears somewhat arbitrary. Are the irregularities referred to a property of the trained networks or would they also emerge with analysis of simulated ideal data? Can more justification be expanded and supplementary analyses be shown when the whole arena is used?

In practical terms, a subsampling of the data to around half was needed because the persistent homology packages struggle to handle large amounts of data, especially in the calculation of H2. We decided to cut a portion of contiguous pixels in the open field at least larger than the hexagonal tile representing the whole grid population period (as represented in Figure 6). Leaving the borders aside was a logical choice since it is known that the solution at the borders is particularly influenced by the speed anisotropy of the virtual rat (see Si, Kropff & Treves, 2012), in a way that mimics how borders locally influence grid maps in actual rats (Krupic et al, 2015). The specific way in which our virtual rat handles borders is arbitrary and might not generalize. A second issue around borders is that maps are differently affected by incomplete smoothing, although this issue does not apply to our data because we did not smooth across neighboring pixels. In sum, considering the central 60 cm wide square was sufficient to contain the whole torus and a reasonable compromise that would allow us to perform all analyses in the part of the environment less influenced by boundaries.

(3) It could help the general reader to briefly explain what a persistence diagram is.

This is developed in the Appendix, but we have now added a reference to it and a brief description in the main text.

(4) For the analyses in Figure 3-4, and separately for Figure 5, it might help the reader to provide visualizations of the low dimensional point cloud.

All these calculations take place in the original high-dimensional point cloud. Doing them in a reduced space would be incorrect because there is no dimensionality reduction technique that guarantees the preservation of topology. In Figure 7 we reduce the dimensionality of data but emphasize that it is only done for visualization purposes, not to characterize topology. We also point out in this Figure that the same non-linear dimensionality reduction technique applied to objects with identical topology yields a wide variety of visualizations, some of them clear and some less clear. This observation further exemplifies why one cannot assume that a dimensionality-reduction technique preserves topology, even for a low-dimensional object embedded in a high-dimensional space.

(5) The detailed comparison of the dynamics of each model is limited by the number of data points. Why not address this by new simulations with more neurons?

We are not sure we understand this comment. In Figure 2, the dynamics for each model are markedly different. These are averages over 100 simulations. We are not sure what benefit would be obtained from adding more neurons. Before starting this work we searched for the minimal number of neurons that would result in convergence to an aligned solution in 2D networks, which we found to be around 100. Optimizing this parameter in advance was important to reduce computational costs throughout our work.

(6) Could the variability in Figure 7 also be addressed by increasing the number of data points?

As we argued in a previous point, there is no reason to expect preservation of topology after applying Isomap. We believe this lack of topology preservation to be the main driver of variability.

(7) Page/line numbers would be useful.

We agree. However, the text is curated by biorxiv which, to our best knowledge, does not include them.

Reviewer 2:

Reviewer #2 (Recommendations For The Authors):

(1) I highly suggest that the author rewrite some parts of the Results. There are lots of details which should be put into the Methods part, for example, the implementation details of the network, the analysis details of the toroidal topology, etc. It will be better to focus on the results part first in each section, and then introduce some of the key details of achieving these results, to improve the readability of the work.

This suggestion contrasts with that of Reviewer #1. As a compromise, we decided to include in the Results section only methodological details that are key to understanding the conclusions, and describe everything else in the Methods section.

(2) 'Progressive increase in gridness and decrease in spacing across days have been observed in animals familiarizing with a novel environment...' From Fig.2c I didn't see much decrease. The authors may need to carry out some statistical test to prove this. Moreover, even the changes are significant, this might be not the consequence of the excitatory collateral constraint. To prove this, the authors may need to offer some direct evidence.

We agree that the decrease is not evident in this figure due to the scale, so we are adding the correlation in the figure caption as proof. In addition, several arguments, some related to new analyses, demonstrate that the attractor contracts grid maps. First, the ‘no attractor’ condition has a markedly larger spacing compared to all other conditions (Fig. 2a). We also now show that spacing monotonically decreases with the strength of recurrent relative to feedforward weights, in a way that is rather independent of gridness (Fig. S2a). Second, as we now show in Fig. S2b-d, simulations with a shuffled 1D attractor, such that the sum of input synapses to each neuron are the same as in the 1D condition but no structure is present, lead to a spacing that is mid-way between the ‘no attractor’ condition and the conditions with attractors. Third, as we now show in Fig. S3a, turning off both recurrent connections and feedforward learning in a trained network results in a small increase in spacing. Fourth, as we now show in Fig. S3b, turning off recurrent connections while feedforward learning is kept on increases grid spacing to levels comparable to those of the ‘no attractor’ condition. All these elements support a role of the attractor in contracting grid spacing.

(3) Some of the items need to be introduced first before going into details in the paper, for instance, the stipe-like attractor network, the Betti number, etc.

We have added in the Results section a brief description and references to full developments in the Appendix.

Reviewer 3 (Public Review):

(1) It is not clear to me that the proposal here is fundamentally new. In Si, Kropff and Treves (2012) recurrent connectivity was dependent on the head direction tuning and thus had a ring structure. Urdapilleta, Si, and Treves considered connectivity that depends on the distance on a 2d plane.

In the work of Si et al connectivity is constructed ad-hoc for conjunctive cells to represent a torus, it depends on head-directionality but also on the distance in a 2D plane. The topology of this architecture has not been assessed, but it is close to the typical 2D ‘rigid’ constraint. In the work of Urdapilleta et al, the network is a simple 2D one. The difference with our work is that we focus on the topology of the recurrent network and do not use head-direction modulation. In this context, we prove that a 1D network is enough to align grid cells and, more generally, we provide a proof of principle that the topology of the architecture and the representation space of an attractor network do not need to be identical, as previously assumed by the attractor community. These two important points were neither argued, speculated nor self-evident from the cited works.

(2) The paper refers to the connectivity within the grid cell layer as an attractor. However, would this connectivity, on its own, indeed sustain persistent attractor states? This is not examined in the paper. Furthermore, is this even necessary to obtain the results in the model? Perhaps weak connections that do not produce an attractor would be sufficient to align the spatial response patterns during the learning of feedforward weights, and reproduce the results? In general, there is no exploration of how the strength of collateral interactions affects the outcome.

The reviewer makes several important points. Local excitation combined with global inhibition is the archetypical architecture for continuous attractors (see for example Knierim and Zhang, Annual review of neuroscience, 2012). Thus, in the absence of feedforward input, we observe a bump of activity. As in all continuous attractors, this bump is not necessarily ‘persistent’ and instead is free to move along the attractor.

We cannot prove that there is not a simpler architecture that has the same effect as our 1D or 1DL conditions, and we think that there are some interesting candidates to investigate in the future. What we now prove in new Fig. S2b-d is that it is not the strength of recurrent connections themselves, but instead the continuous attractor structure that aligns grid cells in our model. To demonstrate this, we shuffle incoming recurrent connections to each neuron in the 1D condition (while avoiding self-connections for fairness), and show that training does not lead to grid alignment. We also show in Fig. S1 that an architecture represented by 20 overlapping 1DL attractors, each formed by concatenating 10 random cells, aligns grid cells to levels slightly lower but similar to the 1D or 1DL attractors. This architecture can perhaps be considered as simpler to build in biological terms than all the others, but it is still constituted by continuous attractors.

The strength of recurrent collaterals, or more precisely the recurrent to feedforward ratio, is crucial in our model to achieve a negotiated outcome from constraints imposed by the attractor and the inputs. We now show explicit measures of this ratio in Fig. S2, as well as examples showing that an imbalance in this ratio impairs grid alignment. When the ratio is too high or too low, both individual and population gridness are low. Interestingly, grid spacing behaves differently, decreasing monotonically with the relative strength of recurrent connections.

(3) I did not understand what is learned from the local topology analysis. Given that all the grid cells are driven by an input from place cells that spans a 2d manifold, and that the activity in the grid cell network settles on a steady state that depends only on the inputs, isn't it quite obvious that the manifold of activity in the grid cell layer would have, locally, a 2d structure?

The dimensionality of the input is important, although not the only determinant of the topology of the activity. The recurrent collaterals are the other determinant, and their architecture is a crucial feature. For example, as we now show in Figure S2b-d, shuffled recurrent synaptic weights fail to align grid cells. In the 1D condition, if feedforward inputs were absent, the dynamics of the activity would be confined to a ring. The opposite condition is our ‘no attractor’ condition, in which activity in the grid cell layer mimics the topology of inputs, a 2D sheet (and not a torus). It is in the intermediate range, when both feedforward and recurrent inputs are important, that a negotiated solution (a torus) is achieved.

The analyses of local dimensionality and local homology of Figure 3 are crucial steps to demonstrate toroidal topology. According to the theorem of classification of closed surfaces, global homology is not enough to univocally define the topology of a point cloud, and thus this step cannot be skipped. The step is aimed to prove that the point cloud is indeed a closed surface.

(4) The modeling is all done in planar 2d environments, where the feedforward learning mechanism promotes the emergence of a hexagonal pattern in the single neuron tuning curve. This, combined with the fact that all neurons develop spatial patterns with the same spacing and orientation, implies even without any topological analysis that the emerging topology of the population activity is a torus.

We cannot agree with this intuition. In the ‘no attractor’ condition, individual maps have hexagonal symmetry with standardized spacing, but given the lack of alignment the population activity is not a closed surface and thus not a torus. It can rather be described as a 2D sheet embedded in a high dimensional space, a description that also applies to the input space.

While it is rather evident that an ad hoc toroidal architecture folds this 2D population activity into a torus, it is less evident and rather surprising that 1D architectures have the same capability. This is the main novelty in our work.

(5) Moreover, the recent work of Gardner et al. demonstrated much more than the preservation of the topology in the different environments and in sleep: the toroidal tuning curves of individual neurons remained the same in different environments. Previous works, that analyzed pairwise correlations under hippocampal inactivation and various other manipulations, also pointed towards the same conclusion. Thus, the same population activity patterns are expressed in many different conditions. In the present model, the results of Figure 6 suggest that even across distinct rectangular environments, toroidal tuning curves will not be preserved, because there are multiple possible arrangements of the phases on the torus which emerge in different simulations.

We agree with the reviewer in the main point, although the recently found ring activity in the absence of sensory feedback (Gonzalo Cogno et al, 2023) suggests that what is happening in the EC is more nuanced than a pre-wired torus. Solutions in Figure 6 are different ways of folding a 1D strip into a torus, with or without the condition of periodicity in the 1D strip. Whether or not these different solutions would be discernible from one another in a practical setup is not clear to us. For example, global homology, as addressed in the Gardner paper, is the same for all these solutions. Furthermore, while our solutions of up to order 3 are highly discernable, higher order solutions, potentially achievable with other network parameters, would be impossible to discern by eye in representations similar to the ones in Figure 6. In addition, while we chose to keep our model in the simplest possible form as a clear proof of principle, new elements introduced to the model such as head directionality could break the symmetry and lead to the prevalence of one preferred solution for all simulation replicates. We plan to investigate this possibility in the future when attempting to incorporate path-integration capabilities to the model.

(6) In real grid cells, there is a dense and fairly uniform representation of all phases (see the toroidal tuning of grid cells measured by Gardner et al). Here the distribution of phases is not shown, but Figure 7 suggests that phases are non uniformly represented, with significant clustering around a few discrete phases. This, I believe, is also the origin for the difficulty in identifying the toroidal topology based on the transpose of the matrix M: vectors representing the spatial response patterns of individual neurons are localized near the clusters, and there are only a few of them that represent other phases. Therefore, there is no dense coverage of the toroidal manifold that would exist if all phases were represented equally. This is not just a technical issue, however: there appears to be a mismatch between the results of the model and the experimental reality, in terms of the phase coverage.

As mentioned in the results section, Figure 7 is meant for visualization purposes only, and serves more as cautionary tale regarding the imprevisible risks of non-linear dimensionality reduction than as a proof of the organization of activity in the network. Isomap is a non-linear transformation that deforms each of our solutions in a unique way so that, while all have the topology of a torus embedded in a high dimensional space, only a few of them exhibited one of two possible toroidal visualizations in a 3D Isomap reduction. Isomap, as well as all other popular dimensionality reduction techniques, provide no guarantee of topology invariance. A better argument to judge the homogenous distribution of phases is persistent homology, which identifies relatively large holes (compared to the sampling spacing) in the original manifold embedded in a high dimensional space. In our case, persistent homology identified only two holes significantly larger than noise (the two cycles of a torus) and one cavity in all conditions that included attractors. Regarding the specific distribution of phases in different conditions, however, see our reply below.

(7) The manuscript makes several strong claims that incorrectly represent the relation between experimental data and attractor models, on one hand, and the present model on the other hand. For the latter, see the comments above. For the former, I provide a detailed list in the recommendations to the authors, but in short: the paper claims that attractor models induce rigidness in the neural activity which is incompatible with distortions seen in the spatial response patterns of grid cells. However, this claim seems to confuse distortions in the spatial response pattern, which are fully compatible with the attractor model, with distortions in the population activity patterns, which would be incompatible with the attractor model. The attractor model has withstood numerous tests showing that the population activity manifold is rigidly preserved across conditions - a strong prediction (which is not made, as far as I can see, by feedforward models). I am not aware of any data set where distortions of the population activity manifold have been identified, and the preservation has been demonstrated in many examples where the spatial response pattern is disrupted. This is the main point of two papers cited in the present manuscript: by Yoon et al, and Gardner et al.

First of all, we would like to note that our model is a continuous attractor model. Different attractor models have different outcomes, and one of the main conclusions of our manuscript is that attractors can do a wider range of operations than previously thought.

We agree with the reviewer that distortions in spatial activity (which speak against a purely path-integration guided attractor) should not be confused with distortions in the topology of the population activity (which would instead speak against the attractor dynamics itself). We have rephrased these observations in the manuscript. In fact, we believe that the capacity of grid cells to present distorted maps without a distortion of the population activity topology, as shown for example by Gardner and colleagues, could result from a tension between feedforward and recurrent inputs, the potential equilibriums of which our manuscript aims to characterize.

(8) There is also some weakness in the mathematical description of the dynamics. Mathematical equations are formulated in discrete time steps, without a clear interpretation in terms of biophysically relevant time scales. It appears that there are no terms in the dynamics associated with an intrinsic time scale of the neurons or the synapses, and this introduces a difficulty in interpreting synaptic weights as being weak or strong. As mentioned above, the nature of the recurrent dynamics within the grid cell network (whether it exhibits continuous attractor behavior) is not sufficiently clear.

We agree with the reviewer that our model is rather simple, and we value the extent to which this simplicity allows for a deep characterization. All models are simplifications and the best model in any given setup is the one with the minimum amount of complexity necessary to describe the phenomenon under study. We believe that to understand whether or not a 1D continuous attractor architecture can result in a toroidal population activity, a biophysically detailed model, with prohibitive computational costs, would have been unnecessarily complex. This argument does not intend to demerit biophysically detailed models, which are capable of addressing a wider range of questions regarding, for example, the spiking dynamics of grid cells, which cannot be addressed by our simple model.

Reviewer #3 (Recommendations For The Authors):

The work points to an interesting scenario for the emergence of toroidal topology, but the interpretation of this idea should be more nuanced. I recommend reconsidering the claims about limitations of the attractor theory, and acknowledging the limitations of the present theory.

I don't see the limitations mentioned above as a reason to reject the ideas proposed in this manuscript, for two main reasons: first, additional research might reveal a regime of parameters where some issues can be resolved (e.g. the clustering of phases). In addition, the mechanism described here might act at an early stage in development to set up initial dynamics along a toroidal manifold, while other mechanisms might be responsible for the rigidity of the toroidal manifold in an adult animal. But all this implies that the novelty in the present manuscript is weaker than implied, the ability to explain experimental observations is more limited than implied, and these limitations should be acknowledged and discussed.

I recommend reporting on the distribution of grid cell phases and, if indeed clustered, this should be discussed. It will be helpful to explore whether this is the reason for the difficulty in identifying the toroidal topology based on the collection of spatial response patterns (using the transpose of the matrix M).

Ideally, a more complete work would also explore in a more systematic and parametric way the influence of the recurrent connectivity's strength on the learning, and whether a toroidal manifold emerges also in non-planar, such as the wagon-wheel environment studied in Gardner et al.

Part of these recommendations have been addressed in the previous points (public review). Regarding the reason why the transpose of M does not fully recapitulate architecture with our conservative classification criteria, we believe that there is no reason why it should in the first place. We view the fact that the transpose of M recapitulates some features of the architecture as a purely phenomenological observation, and we think it is important as a proof that M is not exactly the same for the different conditions. We imagined that if M matrices were exactly the same this could be due to poor spatial sampling by our bins. Knowing that they are intrinsically different is important even if the reason why they have these specific features is not fully clear to us.

Although we do not think that the distribution of phases is related to the absence of a cavity in the transpose of M or to the four clusters found in Isomap projections, it remains an interesting question that we did not explore initially. We are now showing examples of the distribution of phases in Figure S1. We observed that in both 2D and 1D conditions phases are distributed following rather regular patterns. Whether or not these patterns are compatible with experimental observations of phase distribution is to our view debatable, given that so far state-of-the-art techniques have only allowed to simultaneously record a small fraction of the neurons belonging to a given module. This said, we think that it is important to note that ordered phase patterns are an anecdotal outcome of our simulations rather than a necessary outcome of flexible attractors or attractors in general. To prove this point, we simulated a condition with a new architecture represented by the overlap of 20 short 1DL attractors, each recruiting 10 random neurons from the pool of 100 available ones.

The rest of the parameters of the simulations were identical to those in the other conditions.

By definition, the topology of this architecture has Betti numbers [20,0,0]. We show in Figure S1 that this architecture aligns grid cells, with individual and population gridness reaching slightly lower levels compared to the 1D condition. However, the distribution of phases of these grid cells has no discernible pattern. This result is an arbitrary example that serves as a proof-of-principle to show that flexible attractors can align grid cells without exhibiting ordered phases, not a full characterization of the outcome of this type of architecture, which we leave for future work. For the rest of our work, we stick to the simplest versions of 1D architectures, which allow for a more in-depth characterization.

The wagon-wheel is an interesting case in which maps loose hexagonal symmetry although the population activity lies in a torus, perhaps evidencing the tension between feedforward and recurrent inputs and suggesting that grid cell response does not obey the single master of path integration. If we modeled it with a 1D attractor, we believe the outcome would strongly depend on virtual rat trajectory. If the trajectory was strictly linear, the population activity would be locally one-dimensional and potentially represented by a ring. Instead, if the trajectory allowed for turns, i.e. a 2D trajectory within a corridor-like maze, the population activity would be toroidal as in our open field simulations, while maps would not have perfect hexagonal symmetry, mimicking experimental results.

More minor comments:

Recurrent dynamics are modeled as if there is no intrinsic synaptic or membrane time constant. This may be acceptable for addressing the goals of this paper, but it is a bit unusual and it will be helpful to explain and justify this choice.

As mentioned above, we believe that the best model in a given setup is the one with the lowest number of complexities that can still address the phenomenon under study. One does not use general relativity to build a bridge, although it provides a ‘more accurate’ description of the physics involved. All models are simplifications, and the more complex a model, the more it has to be taken as a black box.

The Introduction mentions that in most models interaction between co-modular neurons occurs through direct excitatory communication, but in quite a few models the interaction is inhibitory. The crucial feature is that the interaction is strongly inhibitory between neurons that differ in their tuning, and either less inhibitory or excitatory between neurons with similar phases.

We agree that directed inhibition has been shown to be as efficient as directed excitation, and we have modified the introduction to reflect this.

The Discussion claims that the present work is the first one in which the topology of the recurrent architecture differs from the topology of the emergent state space. However, early works on attractor models of grid cells showed how neural connectivity which is arranged on a 2d plane, without any periodic boundary conditions, leads to a state space that exhibits the toroidal topology. Therefore, this claim should be revised.

We agree, although the 2D sheet in this case acts as a piece of the torus, and locally the input space and architecture are identical objects. It could be argued that architectures that represent a 2D local slice of the torus, the whole torus, or several cycles around the torus form a continuous family parametrized by the extension of recurrent connections, and as a consequence it is not surprising that these works have not made claims about the incongruence between architecture and representation topologies. The 2D sheet connectivity is still constructed ad hoc to organize activity in a 2D bump, and there is no negotiation between disparate constraints because locally the constraints imposed by input and architecture are the same. We believe this situation is conceptually different from our flexible 1D attractors. We have adapted our claim to include this technical nuance.

Why are neural responses in the perimeter of the environment excluded from the topological analysis? The whole point of the toroidal manifold analysis on real experimental data is that the toroidal manifold is preserved regardless of the animal's location and behavioral condition.

We agree, although experimental data needs to go through extensive pre-processing such as dimensionality reduction before showing a toroidal topology. Such manipulations might smooth away the specific effects of boundaries on maps, together with other sources of noise. In our case, the original reason to downsample the dataset is related to the explosion in computational time that we experience with the ripser package when using more than ~1000 data points. For a proof-of-principle characterization we were much more interested in what happened in the center of the arena, where a 1D attractor could fold itself to confine population activity into a torus. The area we chose was sufficiently large to contain the whole torus. Borders do affect the way the attractor folds (they also affect grid maps in real rats). We feel that these imperfections could be interesting to study in relation to the parameters controlling how our virtual rat behaves at the borders, but not at this proof-of-principle stage.

The periodic activity observed in Ref. 29 could in principle provide the basis for the ring arrangement of neurons. However, it is not yet clear whether grid cells participate in this periodic activity.

We agree. So far it seems that entorhinal cells in general participate in the ring, which would imply that all kinds of cells are involved. However, it could well be that only some functional types participate in the ring and grid cells specifically do not, as future experiments will tell.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The main goal of the authors was to study the testis-specific role of the protein FBXO24 in the formation and function of the ribonucleoprotein granules (membraneless electron-dense structures rich in RNAs and proteins).

We appreciate the summary comment of reviewer #1.

Strengths:

The wide variety of methods used to support their conclusions (including transgenic models)

We appreciate the positive comment of reviewer #1.

Weaknesses:

The lack of specific antibodies against FBXO24. Some of the experiments showing a specific phenotype are descriptive and lack of logical explanation about the possible mechanism (i.e. AR or the tail structure).

Because we could not obtain specific antibodies against FBXO24, we generated Fbxo24-FLAG transgenic mice, which can be used to show the interaction between FBXO24 and IPO5. For the mechanism of impaired acrosome reaction, we added some results and discussion as written in the response to the question (1) of reviewer #1 (public review). For the mechanism of abnormal flagellar structure, we added new results and fixed the manuscript as written in the response to the major comments of reviewer #3 (recommendations for the authors).

Questions:

The paper is excellent and employs a wide variety of methods to substantiate the conclusions. I have very few questions to ask:

(1) KO mice cannot undergo acrosome reaction (AR) even spontaneously. How do you account for this, given that no visible defects were observed in the acrosome?

One possibility is that Fbxo24 KO spermatozoa cannot undergo capacitation; however, it is difficult to analyze the capacitation status such as tyrosine phosphorylation because most Fbxo24 KO spermatozoa are not alive (Figure S3A). Other possibility is that AR-related proteins are affected in Fbxo24 KO spermatozoa. Therefore, we analyzed the amounts of AR-related proteins with mass spectrometry (Figure S3C). Although previous studies indicate that the assembly of the SNARE complex is a key event prior to AR [Hutt et al., 2005 (PMID: 15774481); Katafuchi et al., 2000 (PMID: 11066067); Schulz et al., 1997 (PMID: 9356173); Tomes et al., 2002 (PMID: 11884041)], no clear differences were detected for SNARE proteins (Figure S3C and D). PLCD4 that is important for AR [Fukami et al., 2001 (PMID: 11340203)) was also detected in Fbxo24 KO spermatozoa (Figure S3C). Although we could not find differences in the amounts of AR-related proteins, it is still possible that FER1L5, another AR-related protein [Morohoshi et al., 2023 (PMID: 36696506)] not detected in the mass spectrometry analyses, or AR-related proteins not yet identified are affected in Fbxo24 KO spermatozoa. We added these results and discussion (line 160-166 and 305-312).

(2) KO sperm are unable to migrate in the female tract, and, more intriguingly, they do not pass through the utero-tubal junction (UTJ). The levels of ADAM3 are normal, suggesting that the phenotype is influenced by other factors. The authors should investigate the levels of Ly6K since mice also exhibit the same phenotype but with normal levels of ADAM3.

We detected LY6K in Fbxo24 KO spermatozoa with immunoblotting, but no difference was found.

We added the results (Figure S3E and line 172–175).

(3) In Figure 4A, the authors assert that "RBGS Tg mice revealed that mitochondria were abnormally segmented in Fbxo24 KO spermatozoa." I am unable to discern this from the picture shown in that panel. Could you please provide a more detailed explanation or display the information more explicitly?

We are sorry for the ambiguous explanation on the morphology of sperm mitochondria sheath. Fbxo24 KO cauda epidydimal spermatozoa shows disorganized mitochondria sheath rather than “segmented”. We fixed the sentence (line 190-192) and added white arrowheads that indicate the disorganized regions (Figure 4A).

Reviewer #2 (Public Review):

Summary:

The manuscript by Kaneda et al "FBXO24 ensures male fertility by preventing abnormal accumulation of membraneless granules in sperm flagella" is a significant paper on the role of FBXO24 in murine male germ cell development and sperm ultrastructure and function. The body of experimental evidence that the authors present is extraordinarily strong in both breadth and depth. The authors investigate the protein's functions in male germ cells and sperm using a wide variety of approaches but focusing predominantly on their novel mouse model featuring deletion of the Fbxo24 gene and its product. Using this mouse, and a cross of it with another model that expresses reporters in the head and midpiece, they logically build from one experiment to the next. Together, their data show that this protein is involved in the regulation of membraneless electron-dense structures; loss of FBXO24 led to an accumulation of these materials and defects in the sperm flagellum and fertilizing ability. Interestingly, the authors found that several of the best-known components of electron-dense ribonucleoprotein granules that are found in the intermitochondrial cement and chromatoid body were not disrupted in the Fbxo24 knockout, suggesting that the electron-dense material and these structures are not all the same, and the biology is more complicated than some might have thought. They found evidence for the most changes in IPO5 and KPNB1, and biochemical evidence that FBXO24 and IPO5 could interact.

We appreciate the summary comment of reviewer #2.

Strengths:

The authors are to be commended for the thoroughness of their experimental approaches and the extent to which they investigated impacts on sperm function and potential biochemical mechanisms. Very briefly, they start by showing that the Fbxo24 message is present in spermatids and that the protein can interact with SKP1, in a way that is dependent on its F-box domain. This points toward a potential function in protein degradation. To test this, they next made the knockout mouse, validated it, and found the males to be sterile, although capable of plugging a female. Looking at the sperm, they identified a number of ultrastructural and morphological abnormalities, which they looked at in high resolution using TEM. They also cross their model with RBGS mice so that they have reporters in both the acrosome and mitochondria. The authors test a variety of sperm functions, including motility parameters, ability to fertilize by IVF, cumulus-free IVF, zona-free-IVF, and ICSI. They found that ICSI could rescue the knockout but not other assisted reproductive technologies. Defects in male fertility likely resulted from motility disruption and failure to get through the utero-tubal junction but defects in acrosome exocytosis also were noted. The authors performed thorough investigations including both targeted and unbiased approaches such as mass spectrometry. These enabled them to show that although the loss of the FBXO24 protein led to more RNA and elevated levels of some proteins, it did not change others that were previously identified in the electron-dense RNP material.

The manuscript will be highly significant in the field because the exact functions of the electron-dense RNP materials have remained somewhat elusive for decades. Much progress has been made in the past 15 years but this work shows that the situation is more complex than previously recognized. The results show critical impacts of protein degradation in the differentiation process that enables sperm to change from non-descript round cells into highly polarized and compartmentalized mature sperm, with an equally highly compartmentalized flagellum. This manuscript also sets a high bar for the field in terms of how thorough it is, which reveals wide-ranging impacts on processes such as mitochondrial compaction and arrangement in the midpiece, the correct building of the major cytoskeletal elements in the flagellum, etc.

We appreciate the positive comment of reviewer #2.

Weaknesses:

There are no real weaknesses in the manuscript that result from anything in the control of the authors. They attempted to rescue the knockout by expressing a FLAG-tagged Fbxo24 transgene, but that did not rescue the phenotype, either because of inappropriate levels/timing/location of expression, or because of interference by the tag. They also could not make anti-FBXO24 that worked for coimmunoprecipitation experiments, so relied on the FLAG epitope, an approach that successfully showed co-IP with IPO5 and SKP1.

We could not rescue the phenotype with Fbxo24-FLAG transgene, but different Fbxo24 mutant mice show the same phenotypes (Figure S6G). Further, another group showed that Fbxo24 KO mice exhibited abnormal mitochondrial coiling [Li et al., 2024 (PMID: 38470475)], confirming that

FBXO24 is involved in the mitochondrial sheath formation.

Reviewer #3 (Public Review):

Summary:

In this manuscript, the authors found that FBXO24, a testis-enriched F-box protein, is indispensable for male fertility. Fbxo24 KO mice exhibited malformed sperm flagellar and compromised sperm motility.

We appreciate the summary comment of reviewer #3.

Strengths:

The phenotype of Fbxo24 KO spermatozoa was well analyzed.

We appreciate the positive comment of reviewer #3.

Weaknesses:

The authors observed numerous membraneless electron-dense granules in the Fbxo24 KO spermatozoa. They also showed abnormal accumulation of two importins, IPO5 and KPNB1, in the Fbxo24 KO spermatozoa. However, the data presented in the manuscript do not support the conclusion that FBXO24 ensures male fertility by preventing the abnormal accumulation of membraneless granules in sperm flagella, as indicated in the manuscript title.

Fbxo24 KO mice showed abnormal accumulation of membraneless granules in sperm flagella and male infertility, suggesting that FBXO24 is involved in these processes, but there are no results that show the direct relationship as reviewer #3 mentioned. Therefore, we fixed the title.

Recommendations For The Authors:

Reviewer #2 (Recommendations For The Authors):

On page 4, lines 152-154, the authors introduce the RBGS mouse model and use it in their experiments.

However, they left out an obvious but helpful sentence that tells the reader that they crossed the Fbxo24-null mouse with the RBGS. As one continues reading it is clear, but best to avoid even slight confusion.

We revised the explanation in the result section (line 150-153).

Reviewer #3 (Recommendations For The Authors):

In this manuscript, the authors found that FBXO24, a testis-enriched F-box protein, is indispensable for male fertility. Fbxo24 KO mice exhibited malformed sperm flagellar and compromised sperm motility. The phenotype of Fbxo24 KO spermatozoa was well analyzed.

The authors observed numerous membraneless electron-dense granules in the Fbxo24 KO spermatozoa. They also showed abnormal accumulation of two importins, IPO5 and KPNB1, in the Fbxo24 KO spermatozoa. However, the data presented in the manuscript do not support the conclusion that FBXO24 ensures male fertility by preventing the abnormal accumulation of membraneless granules in sperm flagella, as indicated in the manuscript title.

Fbxo24 KO mice showed abnormal accumulation of membraneless granules in sperm flagella and male infertility, suggesting that FBXO24 is involved in these processes, but there are no results that show the direct relationship as reviewer #3 mentioned. Therefore, we fixed the title.

Major comments:

In the title, abstract, introduction, and some sections such as lines 275-276, the authors conclude that FBXO24 prevents the accumulation of importins and RNP granules during spermiogenesis. However, the provided data do not substantiate this claim. To provide conclusive evidence to support the current title, the authors need to present evidence supporting: 1) direct degradation of IPO5 and KPNB1 by FBXO24; 2) the direct requirement of IPO5 for the formation of the membraneless granules, and 3) infertility resulting from the presence of membraneless granules, rather than other issues such as abnormal ODF and AX.

(1) direct degradation of IPO5 and KPNB1 by FBXO24.

To examine if IPO5 can be degraded by FBXO24, we performed a ubiquitination assay using HEK293T cells. Ubiquitination of IPO5 was upregulated in the presence of WT FBXO24 but not with the mutant ΔF-box FBXO24, suggesting that IPO5 can be ubiquitinated by FBXO24. We did not examine the ubiquitination of KPNB1 because we failed to construct a plasmid vector expressing mouse KPNB1. We think that KPNB1 is not the substrate because we did not detect the interaction between FBXO24 and KPNB1 (Figure 5E). We added the results of the ubiquitination assay (Figure

5F and line 261-265) and mentioned it in the abstract (line 35).

(2) the direct requirement of IPO5 for the formation of the membraneless granules.

(3) infertility resulting from the presence of membraneless granules, rather than other issues such as abnormal ODF and AX.

We revealed that IPO5 aggregate under stress condition in COS7 cells (Figure 6C and D); however, we did not examine whether IPO5 is required for the formation of the membraneless granules. We consider that protein degradation systems such as PROTAC or Trim-Away to knockdown IPO5 at the protein level in Fbxo24 KO mice could be a good way to see if the membraneless granules are diminished and male fertility is rescued. However, it takes time to apply the degradation systems in vivo. Therefore, we would like to leave this rescue experiment for future studies. We fixed the title and  abstract (line 37-38), and removed the last sentence of the introduction.

Also, the other group reported the analyses of Fbxo24 KO mice [Li et al., 2024 (PMID: 38470475)] right after we submitted our manuscript to the eLife. They reported not only disorganized flagellar structures but also abnormal head morphology, which may lead to male infertility. The differences from our study may be due to different mouse genetic backgrounds. We mentioned it in the discussion section (line 348-353).

Minor comments:

(1) The authors claimed a significant increase in the total amount of RNAs in Fbxo24 KO spermatozoa (lines 259-261), suggesting that the ...contain RNAs. More direct evidence supporting this claim should be provided.

We show that the amounts of IPO5 and KBNB1 increased in Fbxo24 KO spermatozoa (Figure 5A and B), both of which could be incorporated into RNP granules in COS7 cells (Figure 6C and D), supporting the idea that membraneless electron-dense structures may be RNP granules. However, because we did not show direct evidence that electron-dense structures contain RNAs, we removed the sentences (line 259-261 of the 1st submission manuscript). 

(2) The author should provide an explanation for the absence of a FLAG band in the input Tg in Figure 5D and the larger size of the IPO5 band in the FLAG-IP group compared to the input. Similar observations are also noted in Figure 5E.

The FLAG band is weak because the protein amount is low. When we increase the contrast, we can see the FLAG band. We added an image with high contrast (Figure 5D). Sometimes, proteins run differently with SDS-PAGE after immunoprecipitation, likely due to varying protein composition in the sample. We explained it in the figure legend (line 868-869).

(3) In Line 526, clarify the procedure for sperm purification, and determine the potential for contamination from somatic cells.

We did not perform sperm purification, but when we observed spermatozoa obtained from cauda epididymis, we rarely observed either somatic cells or immature spermatogenic cells. We added  pictures in Figure S7. Further, we added detailed explanation about how to collect spermatozoa from the epididymis (line 549-550).

(4) Define the Y-axis in Figure 2E, F, and G.

We have revised the figures.

Een interessant idee voor de KENSO leesgroep

Lennox argues that both rationality and morality cannot be explained without the Bible & God... Humans are naturally rational and moral beings because "Man are created in God's image" or "The Holy Spirit remains in men"

The Holy Ghost is the reason we can tell right from wrong (spiritual anti-virus)... However, the more we sin, the more we silence this voice in our head until ultimately we cannot hear it anymore.

No person is born a criminal. A killer.

When we get baptized, we effectively restore our connection to God, and thus reenact the Holy Ghost within us; restoring our innocence. Our soul's integrity has been restored and we can hear the Spirit speaking to us loud and clear once again.

As Simone Weil argued, the purpose of a punishment, an adequate one, that is, is to cleanse the taint of our behavior from ourselves... Allowing ourselves to get back into humanity without judgement. Baptism serves the same purpose on a Spiritual level... With the key difference being that it was Christ who endured the ultimate punishment, and by being baptized (willingly), we enjoy that same punishment, can reap its benefits.

smh

-- shaking my head

Going back to the article we read, "Central American Farmers Head to the U.S., Fleeing Climate Change," this could really change these small farms that are struggling financially with investing in sustainability to gain a positive ROI.

We are all united in being human and should act that way. Find common ground rather than focusing on differences. Don't be biased. A house divided will surely fall. A house united is strong.

When humanity is united as one, true societal advancement can happen.

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 and finds no evidence for modulation of cholinergic axons by locomotion velocity. 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.

Author response:

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

Reviewer #1 (Recommendations For The Authors): 

The author has addressed all the concerns I have raised.

I have only one minor suggestion. 

We would argue both a gray screen and a grating are visual stimuli. ... We concur, our data only address one of many possible transitions, but it is a switch between distinct visual stimuli that is sped up by ACh. 

Thank you for clarifying this. 

Following my comment in the previous review, the author has revised the abstract as follows:  (Before) "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." 

(After) "Based on this we speculate that acetylcholine augments the responsiveness of layer 5 neurons to inputs from outside of the local network, possibly enabling faster switching between internal representations during locomotion." 

My previous comment concerned specifically the latter part, "enabling faster switching between internal representations during locomotion", and, in fact, their data fully support the first part, "acetylcholine augments the responsiveness of layer 5 neurons to inputs from outside of the local network". Thus, I suggest the following sentence: 

"Our results suggest that acetylcholine augments the responsiveness of layer 5 neurons to inputs from outside of the local network, possibly enabling faster switching between internal representations during locomotion." 

Thank you for clarifying. We have changed as suggested.

Reviewer #2 (Recommendations For The Authors): 

I thank the authors for the clarification regarding the distribution of running speeds in the study. I do agree that 30 cm/s is indeed fast for head-fixed locomotion. My concern is that while all mice contribute to the low locomotion velocity bin, the high locomotion velocity bin is dominated by a subset of animals, since not all mice reached high locomotion speeds. Therefore, the comparison between low, intermediate and high locomotion velocities includes data from different cohorts of animals and variability across animals may confound the analysis of cholinergic axon activity. However, the manuscript is carefully worded to emphasize lack of evidence (e.g. "we found no evidence of an increase in calcium activity between low and high locomotion velocities") and I have revised my summary in the public review to reflect this. 

I thank the authors for including the scatterplots of single neuron responses locomotion and optogenetic stimulation, which illustrate their heterogeneity. I am surprised that the axes are limited to 20% deltaF/F as visual responses recorded using GCaMP6f often exceed 100% deltaF/F . 

There are definitely neurons with responses larger than 20% dF/F0, but it is a small fraction. There are two considerations relevant to assessing dF/F amplitudes. First, in our hands trial averaged dF/F0 responses tend to be below 30% even for the most responsive neurons (trial averaging convolves response amplitude and response reliability). The reviewer is probably thinking of single trial responses often shown as raw data that can exceed 100s of %. Second, different published variants for calculating dF/F0 can result in a spectrum of values that varies by up to a factor of 10. This is largely a consequence of the choice of F0 and preprocessing related to correcting slow drifts in signal strength (originally motivated by photobleaching). Attempting to compare dF/F0 across labs is unfortunately a futile effort in absence of standardized way of calculating it. 

Allow me to clarify how evaluating the effects of optogenetic stimulation and locomotion without analyzing them at the level of individual neurons could result in misleading conclusions. I will use the effects of cholinergic responses on grating responses as an example but this concern applies equally to the other analyses. The manuscript reports that "in layer 2/3, optogenetic activation of cholinergic axons did not result in a detectable increase in grating onset responses (Figure 4C), while the responses of layer 5 neurons to the same stimulus increased with concurrent optogenetic activation of cholinergic axons." As the Figure R2C-D illustrates, only a minority of L2/3 neurons are excited by the grating in baseline conditions, while the vast majority are either suppressed or non-responsive. This is expected, as it is well established that visual responses in layer 2/3 are sparse. If responses of the small subset of L2/3 neurons that are activated by the grating were enhanced, it may not be apparent in the population average presented in the manuscript. In contrast, since a larger fraction of L5 neurons is excited by the grating, enhancement of grating responses may be easier to detect. In other words, the effects of optogenetic stimulation may be to boost the responses of those neurons that are activated by the grating and the difference between L2/3 and L5 lies simply in the proportion of activated neurons. I do not mean to argue in favour of this specific scenario but simply present it so as to illustrate the way in which considering population averages alone may be misleading. 

While the authors state in their response that "all relevant and clear conclusions are already captured by the mean differences shown in Figure 4", the evidence supporting this statement is not presented in the manuscript. Most importantly, it is essential to determine whether the neurons that show significant activation in response to gratings (Figure 4C-D), mismatch (Figure 4E-F) or locomotion (Figure 4G-H), are affected by optogenetic stimulation in the same way as the population average. 

We have added the analysis suggested as Figure S6. Consistent with the population averages, even within the subset of layer 2/3 neurons most responsive to specific inputs, we found no detectable increase in responsiveness upon optogenetic stimulation of cholinergic axons.

Reviewer #1 (Public Review):

Summary:

Bowler et al. present a thoroughly tested system for modularized behavioral control of navigation-based experiments, particularly suited for pairing with 2-photon imaging but applicable to a variety of techniques. This system, which they name behaviorMate, represents a valuable contribution to the field. As the authors note, behavioral control paradigms vary widely across laboratories in terms of hardware and software utilized and often require specialized technical knowledge to make changes to these systems. Having a standardized, easy-to-implement, and flexible system that can be used by many groups is therefore highly desirable. This work will be of interest to systems neuroscientists looking to integrate flexible head-fixed behavioral control with neural data acquisition.

Strengths:

The present manuscript provides compelling evidence of the functionality and applicability of behaviorMate. The authors report benchmark tests for real-time update speed between the animal's movement and the behavioral control, on both the treadmill-based and virtual reality (VR) setups. Further, they nicely demonstrate and quantify reliable hippocampal place cell coding in both setups, using synchronized 2-photon imaging. This place cell characterization also provides a concrete comparison between the place cell properties observed in treadmill-based navigation vs. visual VR in a single study, which itself is a helpful contribution to the field.

Documentation for installing and operating behaviorMate is available via the authors' lab website and linked in the manuscript.

Weaknesses:

The following comments are mostly minor suggestions intended to add clarity to the paper and provide context for its significance.

(1) As VRMate (a component of behaviorMate) is written using Unity, what is the main advantage of using behaviorMate/VRMate compared to using Unity alone paired with Arduinos (e.g. Campbell et al. 2018), or compared to using an existing toolbox to interface with Unity (e.g. Alsbury-Nealy et al. 2022, DOI: 10.3758/s13428-021-01664-9)? For instance, one disadvantage of using Unity alone is that it requires programming in C# to code the task logic. It was not entirely clear whether VRMate circumvents this disadvantage somehow -- does it allow customization of task logic and scenery in the GUI? Does VRMate add other features and/or usability compared to Unity alone? It would be helpful if the authors could expand on this topic briefly.

(2) The section on "context lists", lines 163-186, seemed to describe an important component of the system, but this section was challenging to follow and readers may find the terminology confusing. Perhaps this section could benefit from an accompanying figure or flow chart, if these terms are important to understand.

(2a) Relatedly, "context" is used to refer to both when the animal enters a particular state in the task like a reward zone ("reward context", line 447) and also to describe a set of characteristics of an environment (Figure 3G), akin to how "context" is often used in the navigation literature. To avoid confusion, one possibility would be to use "environment" instead of "context" in Figure 3G, and/or consider using a word like "state" instead of "context" when referring to the activation of different stimuli.

(3) Given the authors' goal of providing a system that is easily synchronizable with neural data acquisition, especially with 2-photon imaging, I wonder if they could expand on the following features:

(3a) The authors mention that behaviorMate can send a TTL to trigger scanning on the 2P scope (line 202), which is a very useful feature. Can it also easily generate a TTL for each frame of the VR display and/or each sample of the animal's movement? Such TTLs can be critical for synchronizing the imaging with behavior and accounting for variability in the VR frame rate or sampling rate.

(3b) Is there a limit to the number of I/O ports on the system? This might be worth explicitly mentioning.

(3c) In the VR version, if each display is run by a separate Android computer, is there any risk of clock drift between displays? Or is this circumvented by centralized control of the rendering onset via the "real-time computer"?

eLife assessment

This work represents a new toolkit for implementing virtual reality experiments in head-fixed animals. It is a valuable contribution to the field and the evidence for its utility and performance is solid. Some minor improvements in the material presented - including clarifying design decisions and providing more details about design features - would improve the readability and thereby potentially increase its impact.

Reviewer #2 (Public Review):

Summary:

The authors present behaviorMate, an open-source behavior recording and control system including a central GUI and compatible treadmill and display components. Notably, the system utilizes the "Intranet of things" scheme and the components communicate through a local network, making the system modular, which in turn allows user to easily configure the setup to suit their experimental needs. Overall, behaviorMate is a valuable resource for researchers performing head-fixed imaging studies, as the commercial alternatives are often expensive and inflexible to modify.

Strengths and Weaknesses:

The manuscript presents two major utilities of behaviorMate: (1) as an open-source alternative to commercial behavior apparatus for head-fixed imaging studies, and (2) as a set of generic schema and communication protocols that allows the users to incorporate arbitrary recording and stimulation devices during a head-fixed imaging experiment. I found the first point well-supported and demonstrated in the manuscript. Indeed, the documentation, BOM, CAD files, circuit design, source, and compiled software, along with the manuscript, create an invaluable resource for neuroscience researchers looking to set up a budget-friendly VR and head-fixed imaging rig. Some features of behaviorMate, including the computer vision-based calibration of the treadmill, and the decentralized, Android-based display devices, are very innovative approaches and can be quite useful in practical settings. However, regarding the second point, my concern is that there is not adequate documentation and design flexibility to allow the users to incorporate arbitrary hardware into the system. In particular:

(1) The central controlling logic is coupled with GUI and an event loop, without a documented plugin system. It's not clear whether arbitrary code can be executed together with the GUI, hence it's not clear how much the functionality of the GUI can be easily extended without substantial change to the source code of the GUI. For example, if the user wants to perform custom real-time analysis on the behavior data (potentially for closed-loop stimulation), it's not clear how to easily incorporate the analysis into the main GUI/control program.

(2) The JSON messaging protocol lacks API documentation. It's not clear what the exact syntax is, supported key/value pairs, and expected response/behavior of the JSON messages. Hence, it's not clear how to develop new hardware that can communicate with the behaviorMate system.

(3) It seems the existing control hardware and the JSON messaging only support GPIO/TTL types of input/output, which limits the applicability of the system to more complicated sensor/controller hardware. The authors mentioned that hardware like Arduino natively supports serial protocols like I2C or SPI, but it's not clear how they are handled and translated to JSON messages.

Additionally, because it's unclear how easy to incorporate arbitrary hardware with behaviorMate, the "Intranet of things" approach seems to lose attraction. Since currently, the manuscript focuses mainly on a specific set of hardware designed for a specific type of experiment, it's not clear what are the advantages of implementing communication over a local network as opposed to the typical connections using USB.

In summary, the manuscript presents a well-developed open-source system for head-fixed imaging experiments with innovative features. The project is a very valuable resource to the neuroscience community. However, some claims in the manuscript regarding the extensibility of the system and protocol may require further development and demonstration.

Not precisely the direction you're about to go with "god trick," but maybe worth saying: this is a place where dataviz as enlightenment technology betrays its strength and weaknesses. The idea that any reasonable observer would act in the same way from the same evidence is I believe kind of a tenant of enlightenment thinking, and when applied to government leads to a belief that the primary need of governmental reform is to allow the ruler to see the state of their subjects. (My personal head-citation for this is Jeffrey Freedman, The Poisoned Chalice, 2002, which is definitely not the right citation but does probably have links to the canonical works about why the coffeeshop-crowd thought that the world would be saved if they could just get Frederick the Great to read their newspaper.)

In this view one of the things that's interesting about the diagram is not exactly a "god trick" but -- yes I'm a one-trick pony myself -- a "seeing like a state" trick where the conventional naval form of the shipping plan suddenly includes a part of the design of ships that was always there but previously hidden from the state's view -- its morally shocking cargo.

Reviewer #1 (Public Review):

More than ten years ago, it was shown that activity in the primary visual cortex of mice substantially increases when mice are running compared to when they are sitting still. This finding 'revolutionised' our thinking about visual cortex, turning away from it being a passive image processor and highlighting the influence of non-visual factors. The current study now for the first time repeats this experiment in marmosets. The authors find that in contrast to mice, marmoset V1 activity is slightly suppressed during running, and they relate this to differences in gain modulations of V1 activity between the two species.

Strengths

- Replication in primates of the original finding in mice partly took so long, because of the inherent difficulties with recording from the brain of a running primate. In fact one recent, highly related study on macaques looked at spontaneous limb movements as the macaque was sitting. The treadmill for the marmosets in the current study is a very elegant solution to the problem of running in primates. It allows for true replication of the 'running vs stationary' experiment and undoubtedly opens up many possibilities for other experiments recording from a head-fixed but active marmoset.<br /> - In addition to their own data in marmoset, the authors run their analyses on a publicly available data set in mouse. This allows them to directly compare mouse and marmoset findings, which significantly strengthens their conclusions.<br /> - Marmoset vision is fundamentally different from mouse vision as they have a fovea and make goal-directed eye movements. In this revised version of their paper, the authors acknowledge this and investigate the possible effect of eye movements and pupil size on the differences they find between running and stationary. They conclude that eye input does not explain all these differences.

Significance

The paper provides interesting new evidence to the ongoing discussion about the influence of non-visual factors in general, and running in particular, on visual cortex activity. As such, it helps to pull this discussion out of the rodent field mainly and into the field of primate research. The bigger question of *why* there are differences between rodents and primates remains still unanswered, but the authors do their best to provide possible explanations. The elegant experimental set-up of the marmoset on a treadmill will certainly add new findings to this issue also in the years to come.

Reviewer #2 (Public Review):

This work aims at answering whether activity in primate visual cortex is modulated by locomotion, as was reported for mouse visual cortex. The finding that the activity in mouse visual cortex is modulated by running has changed the concept of primary sensory cortical areas. However, it was an open question whether this modulation generalizes to primates.

To answer this fundamental question the authors established a novel paradigm in which a head-fixed marmoset was able to run on a treadmill while watching a visual stimulus on a display. In addition, eye movements and running speed were monitored continuously and extracellular neuronal activity in primary visual cortex recorded using high-channel-count electrode arrays. This paradigm uniquely permitted to investigate whether locomotion modulates sensory evoked activity in visual cortex of marmoset. Moreover, to directly compare the responses in marmoset visual cortex to responses in mouse visual cortex the authors made use of a publicly-available mouse dataset from the Allen Institute. In this dataset the mouse was also running on a treadmill and observing a set of visual stimuli on a display. The authors took extra care to have the marmoset and mouse paradigms as comparable as possible.

To characterize the visually driven activity the authors present a series of moving gratings and estimate receptive fields with sparse noise. To estimate the gain modulation by running the authors split the dataset into epochs of running and non-running which allowed them to estimate the visually evoked firing rates in both behavioral states.

Strengths:

The novel paradigm of head-fixed marmosets running on a treadmill while being presented with a visual stimulus is unique and ideally tailored to answering the question that the authors aimed to answer. Moreover, the authors took extra care to ensure that the paradigm in marmoset matched as closely as possible to the conditions in the mouse experiments such that the results can be directly compared. To directly compare their data the authors re-analyzed publicly available data from visual cortex of mice recorded at the Allen Institute. Such a direct comparison, and reuse of existing datasets, is another strong aspect of the work. Finally, the presented new marmoset dataset appears to be of high quality, the comparison between mouse and marmoset visual cortex is well done and the results and interpretation straightforward.

Weaknesses:

It is known that the locomotion gain modulation varies with layer in mouse visual cortex, with neurons in the infragranular layers expressing a diversity of modulations (Erisken et al. 2014 Current Biology). However, for the marmoset dataset the layer information was unfortunately not recorded, leaving this point open for future studies.

Nonetheless, the aim of comparing the locomotion induced modulation of activity in primate and mouse primary visual cortex was convincingly achieved by the authors. The results shown in the figures support the conclusion that locomotion modulates the activity in primate and mouse visual cortex differently. While mice show a profound gain increase, neurons in primate visual cortex show little modulation or even a reduction in response strength.

This work will have a strong impact on the field of visual neuroscience but also on neuroscience in general. It revives the debate of whether results obtained in the mouse model system can be simply generalized to other mammalian model systems, such as non-human primates. Based on the presented results, the comparison between the mouse and primate visual cortex is not as straightforward as previously assumed. This will likely trigger more comparative studies between mice and primates in the future, which is important and absolutely needed to advance our understanding of the mammalian brain.

Moreover, the reported finding that neurons in primary visual cortex of marmosets do not increase their activity during running is intriguing, as it makes you wonder why neurons in the mouse visual cortex do so. The authors discuss a few ideas in the paper which can be addressed in future experiments. In this regard it is worth noting that the authors report an interesting difference between the foveal and peripheral part of the visual cortex in marmoset. It will be interesting to investigate these differences in more detail in future studies. Likewise, while running might be an important behavioral state for mice, other behavioral states might be more relevant for marmosets and do modulate the activity of primate visual cortex more profoundly. Future work could leverage the opportunities that the marmoset model system offers to reveal new insights about behavioral related modulation in the primate brain.

Reviewer #2 (Public Review):

This paper examined how the activity of neurons in the entopeduncular nucleus (EPN) of mice relates to kinematics, value, and reward. The authors recorded neural activity during an auditory-cued two-alternative choice task, allowing them to examine how neuronal firing relates to specific movements like licking or paw movements, as well as how contextual factors like task stage or proximity to a goal influence the coding of kinematic and spatiotemporal features. The data shows that the firing of individual neurons is linked to kinematic features such as lick or step cycles. However, the majority of neurons exhibited activity related to both movement types, suggesting that EPN neuronal activity does not merely reflect muscle-level representations. This contradicts what would be expected from traditional action selection or action specification models of the basal ganglia.

The authors also show that spatiotemporal variables account for more variability compared to kinematic features alone. Using demixed Principal Component Analysis, they reveal that at the population level, the three principal components explaining the most variance were related to specific temporal or spatial features of the task, such as ramping activity as mice approached reward ports, rather than trial outcome or specific actions. Notably, this activity was present in neurons whose firing was also modulated by kinematic features, demonstrating that individual EPN neurons integrate multiple features. A weakness is that what the spatiotemporal activity reflects is not well specified. The authors suggest some may relate to action value due to greater modulation when approaching a reward port, but acknowledge action value is not well parametrized or separated from variables like reward expectation.

A key goal was to determine whether activity related to expected value and reward delivery arose from a distinct population of EPN neurons or was also present in neurons modulated by kinematic and spatiotemporal features. In contrast to previous studies (Hong & Hikosaka 2008 and Stephenson-Jones et al., 2016), the current data reveals that individual neurons can exhibit modulation by both reward and kinematic parameters. Two potential differences may explain this discrepancy: First, the previous studies used head-fixed recordings, where it may have been easier to isolate movement versus reward-related responses. Second, those studies observed prominent phasic responses to the delivery or omission of expected rewards - responses largely absent in the current paper. This absence suggests a possibility that neurons exhibiting such phasic "reward" responses were not sampled, which is plausible since in both primates and rodents, these neurons tend to be located in restricted topographic regions. Alternatively, in the head-fixed recordings, kinematic/spatial coding may have gone undetected due to the forced immobility.

Overall, this paper offers needed insight into how the basal ganglia output encodes behavior. The EPN recordings from freely moving mice clearly demonstrate that individual neurons integrate reward, kinematic, and spatiotemporal features, challenging traditional models. However, the specific relationship between spatiotemporal activity and factors like action value remains unclear.

Reviewer #1 (Public Review):

The authors in this paper investigate the nature of the activity in the rodent EPN during a simple freely moving cue-reward association task. Given that primate literature suggests movement coding whereas other primate and rodent studies suggest mainly reward outcome coding in the EPNs, it is important to try to tease apart the two views. Through careful analysis of behavior kinematics, position, and neural activity in the EPNs, the authors reveal an interesting and complex relationship between the EPN and mouse behavior.

Strengths:

(1) The authors use a novel freely moving task to study EPN activity, which displays rich movement trajectories and kinematics. Given that previous studies have mostly looked at reward coding during head-fixed behavior, this study adds a valuable dataset to the literature.

(2) The neural analysis is rich and thorough. Both single neuron level and population level (i.e. PCA) analysis are employed to reveal what EPN encodes.

Weaknesses:

(1) One major weakness in this paper is the way the authors define the EPN neurons. Without a clear method of delineating EPN vs other surrounding regions, it is not convincing enough to call these neurons EPNs solely from looking at the electrode cannula track from Figure 2B. Indeed, EPN is a very small nucleus and previous studies like Stephenson-Jones et al (2016) have used opto-tagging of Vglut2 neurons to precisely label EPN single neurons. Wallace et al (2017) have also shown the existence of SOM and PV-positive neurons in the EPN. By not using transgenic lines and cell-type specific approaches to label these EPN neurons, the authors miss the opportunity to claim that the neurons recorded in this study do indeed come from EPN. The authors should at least consider showing an analysis of neurons slightly above or below EPN and show that these neurons display different waveforms or firing patterns.

(2) The authors fail to replicate the main finding about EPN neurons which is that they encode outcome in a negative manner. Both Stephenson-Jones et al (2016) and Hong and Hikosaka (2008) show a reward response during the outcome period where firing goes down during reward and up during neutral or aversive outcome. However, Figure 2 G top panel shows that the mean population is higher during correct trials and lower during incorrect trials. This could be interesting given that the authors might try recording from another part of EPN that has not been studied before. However, without convincing evidence that the neurons recorded are from EPN in the first place (point 1), it is hard to interpret these results and reconcile them with previous studies.

3) The authors say that: 'reward and kinematic doing are not mutually exclusive, challenging the notion of distinct pathways and movement processing'. However, it is not clear whether the data presented in this work supports this statement. First, the authors have not attempted to record from the entire EPN. Thus it is possible that the coding might be more segregated in other parts of EPN. Second, EPNs have previously been shown to display positive firing for negative outcomes and vice versa, something which the authors do not find here. It is possible that those neurons might not encode kinematic and movement variables. Thus, the authors should point out in the main text the possibility that the EPN activity recorded might be missing some parts of the whole EPN.

4). The authors use an IR beam system to record licks and make a strong claim about the nature of lick encoding in the EPN. However, the authors should note that IR beam system is not the most accurate way of detecting licks given that any object blocking the path (paw or jaw-dropping) will be detected as lick events. Capacitance based, closed-loop detection, or video capturing is better suited to detect individual licks. Given that the authors are interested in kinematics of licking, this is important. The authors should either point this out in the main text or verify in the system if the IR beam is correctly detecting licks using a combination of those methods.

Potential risks for alxhermers diase can range from numerous things through out life. head injury, depression, cardiovascular, cerebrovascualr diseas, high parental age at birth, smokinh, increase homcystine- Homocysteine is a type of amino acid. Your body naturally makes it. But at high levels, it can damage the lining of arteries. It can encourage blood clotting. This may raise your risk for coronary artery disease, heart attacks, blood clots, and strokes.

We would like to thank you and the reviewers for your thoughtful comments that assisted us to improve the manuscript. We carefully followed the reviewers’ recommendations and provide a detailed point-by-point account of our responses to the comments. 

Please find below the important changes in the updated manuscript.

(1) We changed the title according to the comments provided by reviewer #1.

(2) We edited the introduction, results, and discussion to improve the link between the objectives of the study, the findings, and their discussion, as reviewer #2 recommended.

(3) We clarified the link between camouflage and fitness, which is now presented as a hypothesis, as reviewer #1 suggested.

(4) We added new analyses and figures in the main text and in the supplementary materials to better emphasize sex differences in landing force, foraging strategies and hunting success, following reviewer #1 suggestion.

(5) According to reviewer #2 comments, we edited the results adding key information about methods to help the reader understand the findings without reading the Methods section.

(6) We added important details about the model selection approach along with a discussion of the low R-square values reported in our analyses on hunting success, as reviewer #2 suggested.

eLife assessment 

This fundamental work substantially advances our understanding of animals' foraging behaviour, by monitoring the movement and body posture of barn owls in high resolution, in addition to assessing their foraging success. With a large dataset, the evidence supporting the main conclusions is convincing. This work provides new evidence for motion-induced sound camouflage and has broad implications for understanding predator-prey interactions. 

Public Reviews: 

Reviewer #1 (Public Review): 

In this paper, Schalcher et al. examined how barn owls' landing force affects their hunting success during two hunting strategies: strike hunting and sit-and-wait hunting. They tracked tens of barn owls that raised their nestlings in nest boxes and utilized high-resolution GPS and acceleration loggers to monitor their movements. In addition, camcorders were placed near their nest boxes and used to record the prey they brought to the nest, thus measuring their foraging success. 

This study generated a unique dataset and provided new insights into the foraging behavior of barn owls. The researchers discovered that the landing force during hunting strikes was significantly higher compared to the sit-and-wait strategy. Additionally, they found a positive relationship between landing force and foraging success during hunting strikes, whereas, during the sit-and-wait strategy, there was a negative relationship between the two. This suggests that barn owls avoid detection by generating a lower landing force and producing less noise. Furthermore, the researchers observed that environmental characteristics affect barn owls' landing force during sit-and-wait hunting. They found a greater landing force when landing on buildings, a lower landing force when landing on trees, and the lowest landing force when landing on poles. The landing force also decreased as the time to the next hunting attempt decreased. These findings collectively suggest that barn owls reduce their landing force as an acoustic camouflage to avoid detection by their prey. 

The main strength of this work is the researchers' comprehensive approach, examining different aspects of foraging behavior, including high-resolution movement, foraging success, and the influence of the environment on this behavior, supported by impressive data collection. The weakness of this study is that the results only present a partial biological story contained within the data. The focus is on acoustic camouflage without addressing other aspects of barn owls' foraging strategy, leaving the reader with many unanswered questions. These include individual differences, direct measurements of owls' fitness, a detailed analysis of the foraging strategy of males and females, and the collective effort per nest box. However, it is possible that these data will be published in a separate paper. 

We greatly appreciate your recognition of the comprehensive approach and extensive data collection. Our primary objective was to study the role of acoustic camouflage. Nonetheless, the manuscript now includes a detailed analysis of the foraging strategy and hunting success of males and females (lines 164-225).

The results presented support the authors' conclusion that lower landing force during sit-andwait hunting increases hunting success, likely due to a decreased probability of detection by their prey, resulting in acoustic camouflage. The authors also argue that hunting success is crucial for survival, and thus, acoustic camouflage has a direct link to fitness. While this statement is reasonable, it should be presented as a hypothesis, as no direct evidence has been provided here.

Thank you for the comment. We agree and thus have edited the language accordingly.  

However, since information about nestling survival is typically monitored when studying behavior during the breeding period, the authors' knowledge of the effect of acoustic camouflage on owls' fitness can probably be provided. Furthermore, it will be interesting to further examine the foraging strategies used by different individuals during foraging, the joint foraging success of both males and females within each nest box, and the link between landing force and foraging success if the data are available.

We are currently writing a manuscript on these topics. We are aware that several scientific questions regarding the foraging ecology of the barn owl still need our attention. Regarding the link between landing force and foraging success, we believe that our revised manuscript addresses this specific topic, please see specific responses below.

However, even without this additional analysis on survival, this paper provides an unprecedented dataset and the first measurement of landing force during hunting in the wild. It is likely to inspire many other researchers currently studying animal foraging behavior to explore how animals' movements affect foraging success.

Reviewer #2 (Public Review): 

Summary: 

The authors provide new evidence for motion-induced sound camouflage and can link the hunting approach to hunting success (detailing the adaptation and inferring a fitness consequence). 

Strengths: 

Strong evidence by combining high-resolution accelerometer data with a ground-truthed data set on prey provisioning at nest boxes. A good set of co-variates to control for some of the noise in the data provides some additional insights into owl hunting attempts. 

Weaknesses: 

There is a disconnect between the hypotheses tested and the results presented, and insufficient detail is provided on the statistical approach. R2 values of the presented models are very small compared to the significance of the effect presented. Without more detail, it is impossible to assess the strength of the evidence.

In the revised manuscript, we changed the way results are presented and we improved the link between the hypotheses and the results. The R2 values are indeed small. It is however important to keep in mind that we are assessing the outcome of one specific behavior (i.e. landing force during sit-and-wait hunts) on hunting success in a wild environment, where many complex ecological interactions likely influence hunting success. Nonetheless, the coefficients (as reported in the results) show that for every 1 N increase in landing force, there is a 15% reduction in hunting success, which is substantial. In the discussion we also note that 50 Hz is a relatively low sampling frequency for estimating the peak ground reaction force. We have gone back over the presentation of our results and made our discussion more nuanced to acknowledge this aspect. 

We have also added a detailed description about our model selection process in the methods section and provide a model selection table for each analysis in the supplementary materials.

The authors seem to overcome persisting challenges associated with the validation and calibration of accelerometer data by ground-truthing on-board measures with direct observations in captivity, but here the methods are not described any further and sample sizes (2 owls - how many different loggers were deployed?) might be too small to achieve robust behavioural classifications.

Thank you for the comment. Details of our methods of behavioural identification are provided in lines 385 – 429. There are two reasons why our results should not be limited by the sample size. First, we used the temporal sequence of changes in acceleration, and rates of change in acceleration data, which make the methods robust to individual differences in acceleration values. Furthermore, our methods for behavioural identification were not based on machine learning. Instead, we use a Boolean based approach (as described in Wilson et al. 2018. MEE), which is more robust to small differences in absolute values that might occur e.g. in relation to slight changes in device position. 

Recommendation for the authors:

Reviewer #1 (Recommendations For The Authors): 

Comment 1. This study provides new insights into animals' foraging behavior and will probably inspire other researchers to examine foraging behavior in such high resolution.

We hope so, thank you.

Comment 2. However, it is necessary to describe better the measured landing force and the hunting strike and perching behavior so the readers can understand these methods when reading the results (and without reading the Methods).

We have now changed the text in the “Results” to help the reader understand the key methods while reading the results.

Comment 3. In addition, make sure you use the same terminology for hunting strategies during the entire paper and especially in all figures and corresponding result descriptions.

We now use consistent terminology throughout the text and figures. We hope that this is now clear in the revised manuscript.

Comment 4. In addition, although I find your statement about the link between acoustic camouflage and fitness reasonable, it should be described as a hypothesis or examined if you want to keep the direct link statement. I believe showing a direct link can add an additional outstanding aspect to this paper, but I also understand that it can be addressed in a separate paper.

We agree that the relationship between hunting success and barn owl fitness is an important topic, but it necessitates a consideration of both hunting strategies, including hunting on the wing, which extends beyond the limits of our current study. Indeed, our primary objective was to conduct a detailed examination of the interplay between acoustic camouflage and the success of the sit-and-wait technique.

However, we have edited the manuscript to explicitly describe the link between acoustic camouflage and fitness as a hypothesis. We believe this adjustment provides a more accurate representation of our approach. We hope this clarifies the specific emphasis of our work and its contribution to the understanding of barn owl hunting behavior.

Here are my detailed comments about the paper: 

Comment 5. Title: Consider changing the title to "Acoustic camouflage predicts hunting success in a wild predator." 

We would like to thank you for your nice proposition. However, we opted for a different title, which is now “Landing force reveals new form of motion-induced sound camouflage in a wild predator”.

Comment 6. Line 91-93: Please provide additional information about the collected dataset, including: 

Description of the total period of observations, an average and standard deviation of perching and hunting attempt events per individual per night, number of foraging trips per individual per night, details about the geographic location and characteristics of the habitat, season, and reproductive state. 

The revised manuscript now includes detailed information about the collected dataset (i.e. study area, reproductive state, etc…). “We used GPS loggers and accelerometers to record high resolution movement data during two consecutive breeding seasons (May to August in 2019 and 2020) from 163 wild barn owls (79 males and 84 females) breeding in nest boxes across a 1,000 km² intensive agricultural landscape in the western Swiss plateau.” Results section, lines 79 – 82

Details about the number of foraging trips per individuals and per night are now presented in the results: “Sexual dimorphism in body mass was marked among our sampled individuals. Males were lighter than females (84 females, average body mass: 322 ± 22.6 g; 79 males, average body mass 281 ± 16.5 g, Fig S6) and provided almost three times more prey per night than females (males: 8 ± 5 prey per night; females: 3 ± 3 prey per night; Fig.S7). Males also displayed higher nightly hunting effort than females (Males: 46 ± 16 hunting attempts per night, n= 79; Females: 25 ± 11 hunting attempts per nights, n=84; Fig. 3A, Fig S8). However, females were more likely to use a sit and wait strategy than males (females: 24% ± 15%, males: 13% ± 10%, Fig.S9). As a result, the number of perching events per night was similar between males and females (Females: 76 ± 23 perching events per nights; Males: 69 ± 20 perching events per night; Fig S8).” (lines 165 – 174) 

Comment 7. In addition, state if the information describes breeding pairs of males and females and provides statistics on the number of tracked pairs and the number of nest boxes.

The revised manuscript now includes a description of the number of tracked breeding pairs and the number of nest boxes. “Of these individuals, 142 belonged to pairs for which data were recovered from both partners (71 pairs in total, 40 in 2019, 31 in 2020). The remaining 21 individuals belonged to pairs with data from one partner (11 females and 1 male in 2019; 4 females and 5 males in 2020).” (lines 82 – 85.)

Comment 8. Line 93: Briefly define the term "landing force" and explain how it was measured (and let the reader know that there is a detailed description in the Methods).

We now include a brief definition of the “landing force” along with a brief explanation of how it was measured in the results section. “We extracted the peak vectoral sum of the raw acceleration during each landing and converted this to ground reaction force (hereafter “landing force”, in Newtons) using measurements of individual body mass (see methods for detailed description).” (lines 92 – 95).

Comment 9. Line 94: All definitions, including "pre-hunting force," need to be better described in the Results section.

Thank you for this suggestion. We now provided a better description of those key definitions directly in the results section: 

Measurement of landing force: “Barn owls employing a sit-and-wait strategy land on multiple perches before initiating an attack, with successive landings reducing the distance to the target prey (Fig. 2C). 

We used the acceleration data to identify 84,855 landings. These were further categorized into perching events (n = 56,874) and hunting strikes (n = 27,981), depending whether barn owls were landing on a perch or attempting to strike prey on the ground (Fig. 1A and B, see methods for specific details on behavioral classification).” (lines 88 – 95)

Pre-hunt perching force predicts hunting success: “Finally, we analyzed whether the landing force in the last perching event before each hunting attempt (i.e. pre-hunt perching force) predicted variation in hunting success” (lines 229 – 230)

Comment 10. Line 102: Remove "Our analysis of 27,981 hunting strikes showed that" and add "n = 27,981" after the statistics. You have already stated your sample size earlier. There is no need to emphasize it again, although your sample size is impressive.

We modified the text in the results section as suggested.

Comment 11. Line 104: The results so far suggest that the difference in landing force between males and females is an outcome of their different body masses. However, it is not clear what is the reason for the difference in the number of hunting strike attempts between males and females (Lines 104-106). Can you compare the difference in landing force between males and females with similar body mass (females from the lower part of the distribution and males from the upper part)? Is there still a difference?

Thank you, following your comment we made some new analyses that clarified the situation around landing force involved in perching and hunting strike events between sexes. But firstly, we wanted to clarify why there is a difference in number of hunting attempts between males and females. During the breeding season, females typically perform most of the incubation, brooding, and feeding of nestlings in the nest, while the male primarily hunts food for the female and chicks. The female supports the male providing food in a very irregular way, and this changes from pair to pair (paper in prep.). The differences in number of hunting attempts between males and females reflects this asymmetry in food provisioning between sexes during this specific period. We specified this in the revised version of the manuscript (lines 164 – 174). 

We also provide a new analysis to investigate sex differences in mass-specific landing force (force/body mass). We found that males and females produce similar force per unit of body mass during perching events. This demonstrates that the overall higher perching force in females (see Fig. 4C in the manuscript) is therefore driven by their higher body mass. (lines 194 – 199)

Comment 12. Line 154: I believe Boonman et al. (2018) is relevant to this part of the discussion. Boonman, Arjan, et al. found that barn owl noise during landing and taking off is worth considering. ["The sounds of silence: barn owl noise in landing and taking off."

Behavioral Processes 157 (2018): 484-488.]

We now cited this paper in the discussion.

Comment 13. Line 164: Your results do not directly demonstrate a link to fitness, although they potentially serve as a proxy for fitness (add a reference). However, you might have information regarding nestlings' survival - that will provide a direct link for fitness. Change your statement or add the relevant data.

We appreciated your feedback, and we adjusted the language accordingly.

Comment 14. Line 213: If the poles are closer to the ground - is it possible that the higher trees and buildings serve for resting and gathering environmental information over greater distances? For example, identifying prey at farther distances or navigating to the next pole?

Yes, this is indeed the most likely explanation for the fact that owls land more on buildings and trees than on poles until the last period (about 6 minutes) before hunting. In these last minutes, barn owls preferentially use poles, as we showed in figure 2B. The revised manuscript now includes this explanation in the discussion (lines 269 – 284).

Comment 15. Line 250: The product "AXY-Trek loggers" does not appear on the Technosmart website (there are similar names, but not an exact match). Are you sure this is the correct name of the tracking device you used? 

Thank you for pointing out this detail that we missed. The device we used is now called "AXY-Trek Mini" (https://www.technosmart.eu/axy-trek-mini/). We have corrected this error directly in the revised manuscript.

Comment 16. Line 256: Please explain how the devices were recovered. Did you recapture the animals? If so, how? Additionally, replace "after approximately 15 days" with the exact average and standard deviation. Furthermore, since you have these data, please state the difference in body mass between the two measurements before and after tagging.

The birds were recaptured to recover the devices. Adults barn owls were recaptured at their nest sites, again using automatic sliding traps that are activated when birds enter the nest box. The statement "after approximately 15 days" was replaced by the exact mean and standard deviation, which were 10.47 ± 2.27 days. Those numbers exclude five individuals from the total of 163 individuals included in this study. They could not be recaptured in the appropriate time window but were re-encountered when they initiated a second clutch later in the season (4 individuals) or a new clutch the year after (1 individual).

We integrated this previously missing information in the revised manuscript (lines 370 – 372).

Comment 17. Line 259: What was the resolution of the camera? What were the recording methods and schedule? How did you analyze these data? 

The resolution was set to 3.1 megapixel. Motion sensitive camera traps were installed at the entrance to each nest box throughout the period when the barn owls were wearing data loggers, and each movement detected triggered the capture of three photos in bursts. The photos recorded were not analyzed as such for this study, but were used to confirm each supply of prey, which had previously been detected from the accelerometer data. We added these details in the revised manuscript (lines 377 – 380)

Comment 18_1. Figure 1: 

Panel A) Include the sex of the described individual. 

The sex of the described individual is now included in the figure caption.

Comment 18_2. It would be interesting to show these data for both males and females from the same nest box (choose another example if you don't have the data for this specific nest box). 

Although we agree that showing tracks of males and females from the same nest is very interesting, the purpose of this figure was to illustrate our data annotation process and we believe that adding too many details on this figure will make it appear messy. However, the revised manuscript now includes a new figure (Fig. 3A) which shows simultaneous GPS tracks of a male and a female during a complete night, with detailed information about perching and hunting behaviors.

Comment 18_3. Add the symbol of the nest box to the legend. 

Done

Comment 18_4. Provide information about the total time of the foraging trip in the text below. 

The duration of the illustrated foraging trip has been included in the figure caption.

Comment 18_5. To enhance the figure’s information on foraging behavior, consider color coding the trajectory based on time and adding a background representing the landscape. Since this paper may be of interest to researchers unfamiliar with barn owl foraging behavior, it could answer some common questions. 

For similar reasons explained in our answer above (Comment 18_2), we would rather keep this figure as clean as possible. However, we followed your recommendations and included these details in the new Figure 3 described above. In this new figure, GPS tracks are color coded according to the foraging trip number and includes a background representing the landscape. To provide even more detail about the landscape, we added another figure in the supplementary materials (Fig. S2) which provides illustration of barn owls foraging ground and nest site that we think might be of interest for people unfamiliar with barn owls.

Comment 18_6. Inset panels) provide a detailed description of the acceleration insert panels. 

Done

Comment 18_7. Color code the acceleration data with different colors for each axis, add x and y axes with labels, and ensure the time frame on the x-axis is clear. How was the self-feeding behavior verified (should be described in the methods section)? 

We kept both inset panels as simple as possible since they serve here as examples, but a complete representation of these behaviors (with time frame, different colors and labels) is provided in the supplementary materials (figure S3). We included this statement in the figure caption and added a reference to the full representations from the supplementary materials: 

In the Figure caption: “Inset panels show an example of the pattern of the tri-axial acceleration corresponding to both nest-box return and self-feeding behaviors (but see Fig S3for a detailed representation of the acceleration pattern corresponding to each behavior).” 

In the Method section: “Self-feeding was evident from multiple and regular acceleration peaks in the surge and heave axes (resulting in peaks in VeDBA values > 0.2 g and < 0.9 g, Fig.S3D), with each peak corresponding to the movement of the head as the prey was swallowed whole.”.

Comment 18_8. Panel B) Note in the caption that you refer to the acceleration z-axis.

We believe that keeping the statement “the heave acceleration…” in the figure caption is more informative than referring to the “z-axis” as it describes the real dimension to which we are referring. The use of the x, y and z axes can be misleading as they can be interchanged depending on the type and setting of recorders used.

Comment 18_9. Present the same time scale for both hunting strategies to facilitate comparison. You can achieve this by showing only part of the flight phase before perching. 

Done

Comment 18_10. Panel C) Presenting the data for both hunting strategy and sex would provide more comprehensive information about the results and would be relatively easy to implement. 

We agree with your comment. We present the differences in landing force for both landing contexts and sexes in the new Figure 3 as well as in the supplementary materials (Figure S10) of this revised manuscript.

Comment 19. Figure 2: Please provide an explanation of the meaning of the circles in the figure caption.  

Done

Comment 20. Figure 3: 

Panel A) It is unclear how the owl illustration is relevant to this specific figure, unlike the previous figures where it is clear. Also, suggest removing the upper black line from the edge of the figure or add a line on the right side. 

Done (now in Figure 2).

Panel B) "Density" should be capitalized. 

Done

Panel C) Add a scale in meters, and it would be helpful to include an indication of time before hunting for each data point. 

Done

Comment 21. Figure S1: Mark the locations of the nest boxes and ensure that trajectories of different individuals and sexes can be identified. 

The purpose of this figure was to show the spatial distribution of the data. We think that adding nest locations and coloring the paths according to individuals and/or sex will make the figure less clear. However, the new Figure 3 highlights those details.

Comment 22. Figure S2: Show the pitch angle similarly to how you showed the acceleration axes, and explain what "VeDBA" stands for. Provide a description of the perching behavior, clearly indicating it on the figure. Add axes (x, y, z) to the illustration of the acceleration explanation. 

We edited this figure (now figure S3) to show the pitch angle and provide an explanation of what “VeDBA” stands for in the figure caption. The figure caption now also provides a better description of the perching behavior. For the axes (i.e. X, Y, Z), we prefer to refer to the heave, surge, and sway as this is more informative and refers to what is usually reported in studies working with tri-axial accelerometers.

Comment 23. Table S1: Improve the explanation in the caption and titles of the table. 

Done

Reviewer #2 (Recommendations For The Authors): 

Comment 1. From the public review and my assessment there, the authors can be assured that I thoroughly enjoyed the read and am looking forward to seeing a revised and improved version of this paper. 

We thank the reviewer for this comment. We revised the manuscript according to their comments.

Comment 2. In addition to my major points stated above, I would like to add the following recommendations: 

The manuscript is overall well written, but it uses a very pictorial language (a little as if we were in a David Attenborough documentary) that I find inappropriate for a research paper (especially in the abstract and introduction, "remarkable" (2x), "sophisticated" (are there any unsophisticated adaptations? We are referring to something under selection after all) etc.

We appreciated that you found the paper overall well written, and we understand the comment about pictorial language. We therefore slightly changed the text to make sure that the adjective used to describe adaptive strategies are not over-emphasized.

Comment 3. Abstract 

"While the theoretical benefits of predator camouflage are well established, no study has yet been able to quantify its consequences for hunting success." - This claim is actually not fully true: 

Nebel Carina, Sumasgutner Petra, Pajot Adrien and Amar Arjun 2019: Response time of an avian prey to a simulated hawk attack is slower in darker conditions, but is independent of hawk colour morph. Soc. open sci.6:190677 

We edited our claim to specify that the consequences of predator camouflage on hunting success has never been quantified in natural conditions and cited the reference in the introduction.

Comment 4. Line 23. Rephrase to: "We used high-resolution movement data to quantify how barn owls (Tyto alba) conceal their approach when using a sit-and-wait strategy, as well as the power exerted during strikes." 

We edited this sentence in the abstract, as suggested.

Comment 5. Results 

There is a disconnect between the objectives outlined at the end of the introduction and the following results that should be improved. 

The authors state: "Using high-frequency GPS and accelerometer data from wild barn owls (Tyto alba), we quantify the landing dynamics of this sit-and-wait strategy to (i) examine how birds adjust their landing force with the behavioral and environmental context and (ii) test the extent to which the magnitude of the predator cue affects hunting success." But one of the first results presented are sex differences. 

This is a fair point. We have now changed our statement in the end of the introduction as well as the order of the results to improve the link between the objectives outlined in the introduction and the way result are presented. 

Comment 6. At this stage, the reader does not even know yet that we are presented with a size-dimorphic species that also has very different parental roles during the breeding season. This should be better streamlined, with an extra paragraph in the introduction. And these sex differences are then not even discussed, so why bring them up in the first place (and not just state "sex has been fitted as additional co-variate to account for the size-dimorphism in the species" without further details). 

We edited the way the objectives are outlined in the introduction to cover the size dimorphism (lines 70 – 76). We also completely changed the way the sex differences are presented in the results, including a new analysis that we believe provides a better comprehensive understanding of barn owl foraging behavior (lines 164 – 206). Finally, we added a new paragraph in the discussion to consider those results (lines 319 – 339).

Comment 7. It is not clear to me where and how high-resolution GPS data were used? The results seem to concentrate on ACC – why GPS was used and how it features should be foreshadowed in a few lines in the introduction. I definitively prefer having the methods at the end of a manuscript, but with this structure, it is crucial to give the reader some help to understand the storyline. 

GPS data were used to validate some behavioral classifications (prey provisioning for example), but most importantly they were used to link each landing event with perch types. We edited the text in the result section to clarify where GPS and/or ACC data were used.

Comment 8. Discussion 

Move the orca example further down, where more detail can be provided to understand the evidence. 

After our extensive edits in the discussion, we felt this example was interrupting the flow. We now cite this study in the introduction. 

Comment 9. Size dimorphism and evident sex differences are not discussed. 

The revised manuscript now includes a new paragraph in the discussion in which sex differences are discussed (lines 319 – 339).

Comment 10. Be more precise in the terminology used (for example, land use seems to be interchangeable with habitat characteristics?). 

We modified “land use” with “habitat data” in the revised manuscript.

Comment 11. Methods 

Please provide a justification for the very high weight limit (5%; line 256). This limit is outdated and does not fulfill the international standard of 3% body weight. I assume the ethics clearance went through because of the short nature of the study (i.e., the birds were not burdened for life with the excess weight? But a line is needed here or under the ethics considerations to clarify this). 

The 5% weight limit was considered acceptable due to the short deployment period, and we now edited the ethics statement to emphasize this point. However, it is important to note that there is no real international standard, with both 3% and 5% weight limits being commonly used. Both limits are arbitrary and the impact of a fixed mass on a bird varies with species and flight style. All owls survived and bred similarly to the non-tagged individuals in the population (lines 373 – 376 & lines 558 – 561)

EDITORIAL COMMENT: We strongly encourage you to provide further context and clarification on this issue, as suggested by the Reviewer. On a related point, the ethics statement refers to GPS loggers, rather than GPS and ACC devices; we encourage you to clarify wording here.

Thank you for highlighting this point that indeed needed some clarifications.

Although we have used the terminology "GPS recorders", the authorization granted by the Swiss authorities for this study effectively covers the entire tracking system, which combines both GPS and ACC recorders in the same device. We have therefore changed the wording used in the ethics statement to avoid any misunderstanding (lines 373 – 376 & lines 558 – 561)

Comment 12. Please provide more information on the model selection approach, what does "Non-significant terms were dropped via model simplification by comparing model AIC with and without terms." mean? Did the authors use a stepwise backward elimination procedure (drop1 function)? Or did they apply a complete comparison of several candidate models? I think a model comparison approach rather than stepwise selection would be more informative, as several rather than only one model could be equally probable. This might also improve model weights or might require a model averaging procedure - current reported R2values are very small and do not seem to support the results well. 

We apologize for the lack of details about this important aspect of the statistical analysis. We applied an automated stepwise selection using the dredge function from the R package “MuMin”, therefore applying a complete comparison of several candidate models. The final models were chosen as the best models since the number of candidate models within ∆AIC<2 was relatively low in each analysis and thus a model averaging was not appropriate here. We edited the methods section to ensure clarity, and added model selection tables for each analysis, ranked according to AICc scores, in the supplementary materials (lines 532 – 552)

In addition, we agree that the reported R-squared values in our analyses are quite low, specifically regarding the influence of pre-hunt perching force on hunting success (cond R2 = 0.04). Nonetheless, landing impact still has a notable effect size (an increase of 1N reduces hunting success by 15%). The reported values are indicative of the inherent complexity in studying hunting behavior in a wild setting where numerous variables come into play. We specifically investigated the hypothesis that the force involved during pre-hunt landings, and consequently the emitted noise, influences the success of the next hunting attempt in wild barn owls. Factors such as prey behavior and micro-habitat characteristics surrounding prey (such as substrate type and vegetation height) are most likely to be influential but hard, or nearly impossible, to model. We now cover this in a more nuanced way in the discussion (lines 266 – 268)

Comment 13. Please explain why BirdID was nested in NightID - this is not clear to me.

Probably here there is a misunderstanding because we wrote that we nested NightID in BirdID (and not BirdID in NightID). 

Comment 14. I hope the final graphs and legends will be larger, they are almost impossible to read. 

We enlarged the graphs and legends as much as possible to improve readability. However, looking at the graphs in the published version they seem clear and readable.

Comment 15. Figure S1: Does "representation" mean the tracks don't show all of the 163 owls? If so, be precise and tell us how many are illustrated in the figure. 

Figure S1 represent the tracks for each of the 163 barn owls used in the study. We changed the terminology used in the figure caption to avoid any misunderstanding.

Comment 16. Figure S4: Please adjust the y-axis to a readable format. 

Done

Reviewer #1 (Public Review):

Summary:

In this study, Floedder et al report that dopamine ramps in both Pavlovian and Instrumental conditions are shaped by reward interval statistics. Dopamine ramps are an interesting phenomenon because at first glance they do not represent the classical reward prediction errors associated with dopamine signaling. Instead, they seem somewhat to bridge the gap between tonic and phasic dopamine, with an intense discussion still being held in the field about what is their actual behavioral role. Here, in tests with head-fixed mice, and dopamine being recorded with a genetically encoded fluorescent sensor in the nucleus accumbens, the authors find that dopamine ramps were only present when intertrial intervals were relatively short and the structure of the task (Pavlovian cue or progression in a VR corridor) contained elements that indicated progression towards the reward (e.g., a dynamic cue). The authors show that these findings are well explained by their previously published model of Adjusted Net Contingency of Causal Relation (ANCCR).

Strengths:

This descriptive study delineates some fundamental parameters that define dopamine ramps in the studied conditions. The short, objective, and to-the-point format of the manuscript is great and really does a service to potential readers. The authors are very careful with the scope of their conclusions, which is appreciated by this reviewer.

Weaknesses:

The discussion of the results is very limited to the conceptual framework of the authors' preferred model (which the authors do recognize, but it still is a limitation). The correlation analysis presented in panel I of Figure 3 seems unnecessary at best and could be misleading, as it is really driven by the categorical differences between the two conditions that were grouped for this analysis. There are some key aspects of the data and their relationship with each other, the previous literature, and the methods used to collect them, that could have been better discussed and explored.

line 6 supposed to print out 2 right? work 2/3 or do it in your head and its 2 lol not 3 (as remainder)

To ensure that all code snippets are visible to everyone but only the user who created a snippet can update or delete it, you can create a custom permission class. This custom permission will be added to the snippet instance endpoint to enforce these rules.

Step-by-Step Instructions

1. Create Custom Permission Class: Create a new file called permissions.py in your snippets app directory and define a custom permission class IsOwnerOrReadOnly.

2. Update View to Use Custom Permission: Modify the SnippetDetail view to use the custom permission class in addition to the IsAuthenticatedOrReadOnly permission class.

Step 1: Create Custom Permission Class

snippets/permissions.py

```python from rest_framework import permissions

class IsOwnerOrReadOnly(permissions.BasePermission): """ Custom permission to only allow owners of an object to edit it. """

def has_object_permission(self, request, view, obj):
    # Read permissions are allowed to any request,
    # so we'll always allow GET, HEAD or OPTIONS requests.
    if request.method in permissions.SAFE_METHODS:
        return True

    # Write permissions are only allowed to the owner of the snippet.
    return obj.owner == request.user

```

Step 2: Update the View to Use Custom Permission

views.py

First, import the custom permission class at the top of your views.py file:

python from snippets.permissions import IsOwnerOrReadOnly

Then, update the SnippetDetail view to include the custom permission in the permission_classes property:

```python from rest_framework import generics from rest_framework import permissions from .models import Snippet from .serializers import SnippetSerializer

class SnippetList(generics.ListCreateAPIView): queryset = Snippet.objects.all() serializer_class = SnippetSerializer permission_classes = [permissions.IsAuthenticatedOrReadOnly]

def perform_create(self, serializer):
    serializer.save(owner=self.request.user)

class SnippetDetail(generics.RetrieveUpdateDestroyAPIView): queryset = Snippet.objects.all() serializer_class = SnippetSerializer permission_classes = [permissions.IsAuthenticatedOrReadOnly, IsOwnerOrReadOnly] ```

Explanation of the Code

• Custom Permission Class (IsOwnerOrReadOnly):
• permissions.BasePermission: This is the base class for all permissions in Django REST Framework.

• has_object_permission: This method checks whether the request has the required permissions for a specific object.

  • Read Permissions: Always allow safe methods (GET, HEAD, OPTIONS).
  • Write Permissions: Only allow if the user making the request is the owner of the object.

• SnippetDetail View:

• permission_classes: Combines IsAuthenticatedOrReadOnly (which allows read access to everyone and write access only to authenticated users) with IsOwnerOrReadOnly (which restricts write access to the owner of the snippet).

What Happens Now

• Read Access: Any user (authenticated or not) can read (list and retrieve) snippets.
• Write Access: Only authenticated users can create snippets, and only the owner of a snippet can update or delete it.

Testing the Setup

1. Open the Browsable API: Navigate to a snippet instance endpoint in your browser.
2. Check Actions: You should see the 'DELETE' and 'PUT' actions only if you are logged in as the user who created the snippet.

Summary

• Purpose: Ensure all code snippets are visible to everyone, but only the creator can update or delete their snippets.
• Implementation: Create a custom permission class and apply it to the SnippetDetail view.
• Result: Proper access control is enforced, allowing only the snippet owner to modify their snippet while everyone can read the snippets.

This setup ensures that your API adheres to the required permissions, providing both visibility and security.

Reviewer1: Arvind Varsani The MS titled "Hecatomb: An Integrated Software Platform for Viral Metagenomics" addresses the developed of a toolkit for viral meatgenomics analysis that assembles a variety of tools into a workflow.Overall, I do not have any issue with this MS or the toolkit.I have some minor points to help improve the MS and make it as current as possible.1. Line 40: I would include Cenote-take 2 PMID: 33505708, geNomad https://www.biorxiv.org/content/10.1101/2023.03.05.531206v12. Line 40: I would probably not cite the preprint of this current paper - see ref 21.3. Line 80: Actually Cenote-take (both version 1 and 2) both use HHMs and as far as I know so does geNomad.4. Line 248: Please note that Siphoviridae, Podoviridae and Myoviridae are not currently family names. See PMID: 366830755. This means you will likely need to edit you figure to collapse these to Caudovirales6. Line 250-251: Picornaviridae and Adenoviridiae should be in italics7. Line 270: Here and elsewhere, please note that a taxa do not infect a host, it is a virus that infects a host. "Mimiviridae, that infect Acanthamoeba, and Phycodnaviridae, that infect algae, are both dsDNA viruses with large genomes" should ideally be written as "Viruses in the family Mimiviridae infect Acanthamoeba and those in the family Phycodnavirida infect algae, are dsDNA viruses with large genomes."8. Figure 6: the name tags of the CDS/ ORFS are truncated e.g. replication initiate…, heat maturation prot…9. Figure 6: Major head protein should be major capsid protein.10. One thing that I would highlight is that none of the workflows / tool kits developed account for spliced CDS. This is a major issue in automation of virus genome annotation at the moment and with this there will be some degree of misidentification for taxa assignment.

The Mongol customs rely heavily on alcohol and the relationship around the master. They would appear more superstitious at first but seem more prayer-like in some ways. specifically, when pouring exactly three sprinkles in the South, East, West, and North to give reverence to the fire, air, water, and the dead. It's fascinating to see how different customs hold high regard in their prayers and respect for their masters.

NOOKOEPW;SA DkkkkkkPW4TH8IL C

NOOO

disgusting

thats kinda hot

just like he made bran look

alicent would love him

oh he really needs a hug

not her having to do those acts for him :(

ohh nah not the jean de arc bob

UFINW LITTLEFINGER WHEN I CATCH YOU

JON IS MY SON IDCC

oh i hate them all

YES CAT

theyre a fun pair

the dreams...

fr

now thats a REAL leader

yess waymar

So often in the schools I have been in coaching is seen as more of a burden. While many teachers would say their coaches give them good advice, the coaching is also a major source of stress for already overwhelmed teachers. I wonder how to shift this practice so that this "my head would not be above water without my coach" can be a reality.

MDMA-assisted therapy for severe PTSD: a randomized, double-blind, placebo-controlled phase 3 study

• Jennifer M. Mitchell, 
• Michael Bogenschutz, 
• Alia Lilienstein, 
• Charlotte Harrison, 
• Sarah Kleiman, 
• Kelly Parker-Guilbert, 
• Marcela Ot'alora G., 
• Wael Garas, 
• Casey Paleos, 
• Ingmar Gorman, 
• Christopher Nicholas, 
• Michael Mithoefer, 
• Shannon Carlin, 
• Bruce Poulter, 
• Ann Mithoefer, 
• Sylvestre Quevedo, 
• Gregory Wells, 
• Sukhpreet S. Klaire, 
• Bessel van der Kolk, 
• Keren Tzarfaty, 
• Revital Amiaz, 
• Ray Worthy, 
• Scott Shannon, 
• Joshua D. Woolley, 
• ...
• Rick Doblin 

Show authors

Nature Medicine volume 27, pages1025--1033 (2021)Cite this article

• 626k Accesses

• 437 Citations

• 4858 Altmetric

• Metricsdetails

Matters Arising to this article was published on 11 October 2021

Matters Arising to this article was published on 11 October 2021

Abstract

Post-traumatic stress disorder (PTSD) presents a major public health problem for which currently available treatments are modestly effective. We report the findings of a randomized, double-blind, placebo-controlled, multi-site phase 3 clinical trial (NCT03537014) to test the efficacy and safety of 3,4-methylenedioxymethamphetamine (MDMA)-assisted therapy for the treatment of patients with severe PTSD, including those with common comorbidities such as dissociation, depression, a history of alcohol and substance use disorders, and childhood trauma. After psychiatric medication washout, participants (n = 90) were randomized 1:1 to receive manualized therapy with MDMA or with placebo, combined with three preparatory and nine integrative therapy sessions. PTSD symptoms, measured with the Clinician-Administered PTSD Scale for DSM-5 (CAPS-5, the primary endpoint), and functional impairment, measured with the Sheehan Disability Scale (SDS, the secondary endpoint) were assessed at baseline and at 2 months after the last experimental session. Adverse events and suicidality were tracked throughout the study. MDMA was found to induce significant and robust attenuation in CAPS-5 score compared with placebo (P < 0.0001, d = 0.91) and to significantly decrease the SDS total score (P = 0.0116, d = 0.43). The mean change in CAPS-5 scores in participants completing treatment was -24.4 (s.d. 11.6) in the MDMA group and -13.9 (s.d. 11.5) in the placebo group. MDMA did not induce adverse events of abuse potential, suicidality or QT prolongation. These data indicate that, compared with manualized therapy with inactive placebo, MDMA-assisted therapy is highly efficacious in individuals with severe PTSD, and treatment is safe and well-tolerated, even in those with comorbidities. We conclude that MDMA-assisted therapy represents a potential breakthrough treatment that merits expedited clinical evaluation.

Similar content being viewed by others

MDMA-assisted therapy for moderate to severe PTSD: a randomized, placebo-controlled phase 3 trial

Article Open access14 September 2023

Trauma-focused treatment for comorbid post-traumatic stress and substance use disorder

Article 14 November 2022

Behavioral and neurocognitive factors distinguishing post-traumatic stress comorbidity in substance use disorders

Article Open access14 September 2023

Main

PTSD is a common and debilitating condition with immeasurable social and economic costs that affects the lives of hundreds of millions of people annually. There are a number of environmental and biological risk factors that contribute to the development and maintenance of PTSD1, and poor PTSD treatment outcomes are associated with several comorbid conditions that include childhood trauma2, alcohol and substance use disorders3, depression4, suicidal ideation5 and dissociation6. It is therefore imperative to identify a therapeutic that is beneficial in those individuals with the comorbidities that typically confer treatment resistance.

The selective serotonin reuptake inhibitors (SSRIs) sertraline and paroxetine are Food and Drug Administration (FDA)-approved first-line therapeutics for the treatment of PTSD. However, an estimated 40--60% of patients do not respond to these compounds7. Likewise, although evidenced-based trauma-focused psychotherapies such as prolonged exposure and cognitive behavioral therapy are considered to be the gold standard treatments for PTSD8, many participants fail to respond or continue to have significant symptoms, and dropout rates are high9,10. Novel cost-effective therapeutics are therefore desperately needed11.

The substituted amphetamine 3,4-methylenedioxymethamphetamine (MDMA) induces serotonin release by binding primarily to presynaptic serotonin transporters12. MDMA has been shown to enhance fear memory extinction, modulate fear memory reconsolidation (possibly through an oxytocin-dependent mechanism), and bolster social behavior in animal models13,14. Pooled analysis of six phase 2 trials of MDMA-assisted therapy for PTSD have now shown promising safety and efficacy findings15.

Here, we assess the efficacy and safety of MDMA-assisted therapy in individuals with severe PTSD. Participants were given three doses of MDMA or placebo in a controlled clinical environment and in the presence of a trained therapy team. Primary and secondary outcome measures (CAPS-5 and SDS, respectively) were assessed by a centralized pool of blinded, independent diagnostic assessors. MDMA-assisted therapy for PTSD was granted an FDA Breakthrough Therapy designation, and the protocol and statistical analysis plan (SAP) were developed in conjunction with the FDA16.

Results

Demographics

Participants were recruited from 7 November 2018 to 26 May 2020, with the last participant visit conducted on 21 August 2020. A total of 345 participants were assessed for eligibility, 131 were enrolled, 91 were confirmed for randomization (United States, n = 77; Canada, n = 9; Israel, n = 5), and 46 were randomized to MDMA and 44 to placebo (Fig. 1).

Fig. 1: Procedure timeline and study flow diagram.

a, Procedure timeline. Following the screening procedures and medication taper, participants attended a total of three preparatory sessions, three experimental sessions, nine integration sessions and four endpoint assessments (T1--4) over 18 weeks, concluding with a final study-termination visit. IR, independent rater; T, timepoint of endpoint assessment; T1, baseline; T2, after the first experimental session; T3, after the second experimental session; T4, 18 weeks after baseline. b, CONSORT diagram indicating participant numbers and disposition through the course of the trial.

Full size image

Study arms were not significantly different in terms of race, ethnicity, sex, age, dissociative subtype, disability or CAPS-5 score (Table 1). The mean duration of PTSD diagnosis was 14.8 (s.d. 11.6) years and 13.2 (s.d. 11.4) years in the MDMA and placebo groups, respectively. Of note, six participants in the MDMA group and 13 participants in the placebo group had the dissociative subtype according to CAPS-5 score.

Table 1 Demographics and baseline characteristics

Full size table

Efficacy

MDMA significantly attenuated PTSD symptomology, as shown by the change in CAPS-5 total severity score from baseline to 18 weeks after baseline. Mixed model repeated measure (MMRM) analysis of the de jure estimand (that is, the effects of the drug if taken as directed) showed a significant difference in treatment arms (n = 89 (MDMA n = 46), P < 0.0001, between-group difference = 11.9, 95% confidence interval (CI) = 6.3--17.4, d.f. = 71) (Fig. 2a). MMRM sensitivity analysis of the de facto estimand (that is, the effects of the drug if taken as assigned, regardless of adherence) showed a significant difference in treatment arms (n = 90, P < 0.0001, d.f. = 72).

Fig. 2: Measures of MDMA efficacy in the MDMA-assisted therapy group and the placebo group.

a, Change in CAPS-5 total severity score from T1 to T4 (P < 0.0001, d = 0.91, n = 89 (MDMA n = 46)), as a measure of the primary outcome. Primary analysis was completed using least square means from an MMRM model. b, Change in SDS total score from T1 to T4 (P = 0.0116, d = 0.43, n = 89 (MDMA n = 46)), as a measure of the secondary outcome. Primary analysis was completed using least square means from an MMRM model. c, Change in BDI-II score from T1 to study termination (t = -3.11, P = 0.0026, n = 81 (MDMA n = 42)), as a measure of the exploratory outcome. Data are presented as mean and s.e.m.

Full size image

The mean change in CAPS-5 scores from baseline to 18 weeks after baseline in the completers (per protocol set) was -24.4 (s.d. 11.6) (n = 42) in the MDMA-assisted therapy group compared with -13.9 (s.d. 11.5) (n = 37) in the placebo with therapy group.

The effect size of the MDMA-assisted therapy treatment compared with placebo with therapy was d = 0.91 (95% CI = 0.44--1.37, pooled s.d. = 11.55) in the de jure estimand and d = 0.97 (95% CI = 0.51--1.42) in the de facto estimand. When the within-group treatment effect (which included the effect of the supportive therapy that was administered in both arms) was compared between the MDMA and placebo groups, the effect size was 2.1 (95% CI = -5.6 to 1.4) in the MDMA group and 1.2 (95% CI = -4.9 to 2.5) in the placebo group.

Over the same period, MDMA significantly reduced clinician-rated functional impairment as assessed with the SDS. MMRM analysis of the de jure estimand showed a significant difference in treatment arms (n = 89 (MDMA n = 46), P = 0.0116, d.f. = 71, effect size = 0.43, 95% CI = -0.01 to 0.88, pooled s.d. = 2.53) (Fig. 2b). The mean change in SDS scores from baseline to 18 weeks after baseline in the completers was -3.1 (s.d. 2.6) (n = 42) in the MDMA-assisted therapy group and -2.0 (s.d. 2.4) (n = 37) in the placebo with therapy group.

MDMA was equally effective in participants with comorbidities that are often associated with treatment resistance. Participants with the dissociative subtype of PTSD who received MDMA-assisted therapy had significant symptom reduction on the CAPS-5 (mean MDMA Δ = -30.8 (s.d. 9.0), mean placebo Δ = -12.8 (s.d. 12.8)), and this was similar to that in their counterparts with non-dissociative PTSD (mean MDMA Δ = -23.6 (s.d. 11.7), mean placebo Δ = -14.3 (s.d. 11.2)). The benefit of MDMA therapy was not modulated by history of alcohol use disorder, history of substance use disorder, overnight stay or severe childhood trauma. Results were consistent across all 15 study sites with no effect by study site (P = 0.1003). In MMRM analysis there was no obvious impact of SSRI history on effectiveness of MDMA (Supplementary Table 2).

MDMA therapy was effective in an exploratory endpoint analysis of the reduction of depression symptoms (using the Beck Depression Inventory II (BDI-II)) from baseline to study termination of the de jure estimand (mean MDMA Δ = -19.7 (s.d. 14.0), n = 42; mean placebo Δ = -10.8 (s.d. 11.3), n = 39; t = -3.11, P = 0.0026, d.f. = 79, effect size = 0.67, 95% CI = 0.22--1.12) (Fig. 2c).

Clinically significant improvement (a decrease of ≥10 points on the CAPS-5), loss of diagnosis (specific diagnostic measure on the CAPS-5), and remission (loss of diagnosis and a total CAPS-5 score ≤ 11) were each tracked. At the primary study endpoint (18 weeks after baseline), 28 of 42 (67%) of the participants in the MDMA group no longer met the diagnostic criteria for PTSD, compared with 12 of 37 (32%) of those in the placebo group after three sessions. Additionally, 14 of 42 participants in the MDMA group (33%) and 2 of 37 participants in the placebo group (5%) met the criteria for remission after three sessions (Fig. 3).

Fig. 3: Treatment response and remission for MDMA and placebo groups as a percentage of total participants randomized to each arm (MDMA, n = 46; placebo, n = 44).

Responders (clinically significant improvement, defined as a ≥10-point decrease on CAPS-5), loss of diagnosis (specific diagnostic measure on CAPS-5), and remission (loss of diagnosis and a total CAPS-5 score of ≤11) were tracked in both groups. Non-response is defined as a <10-point decrease on CAPS-5. Withdrawal is defined as a post-randomization early termination.

Full size image

Safety

Treatment-emergent adverse events (TEAEs, adverse events that occurred during the treatment period from the first experimental session to the last integration session) that were more prevalent in the MDMA study arm were typically transient, mild to moderate in severity, and included muscle tightness, decreased appetite, nausea, hyperhidrosis and feeling cold (Supplementary Table 3). Importantly, no increase in adverse events related to suicidality was observed in the MDMA group. A transient increase in vital signs (systolic and diastolic blood pressure and heart rate) was observed in the MDMA group (Supplementary Table 4). Two participants in the MDMA group had a transient increase in body temperature to 38.1 °C: one had an increase after the second MDMA session, and one had an increase after the second and third MDMA sessions.

Two participants, both randomized to the placebo group, reported three serious adverse events (SAEs) during the trial. One participant in the placebo group reported two SAEs of suicidal behavior during the trial, and another participant in the placebo group reported one SAE of suicidal ideation that led to self-hospitalization. Five participants in the placebo group and three participants in the MDMA group reported adverse events of special interest (AESIs) of suicidal ideation, suicidal behavior or self-harm in the context of suicidal ideation. One participant in the placebo group reported two cardiovascular AESIs in which underlying cardiac etiology could not be ruled out (Table 2). One participant randomized to the MDMA group chose to discontinue participation due to being triggered by the CAPS-5 assessments and to an adverse event of depressed mood following an experimental session; this participant met the criterion as a non-responder, which was defined as having a less than 10-point decrease in CAPS-5 score. MDMA sessions were not otherwise followed by a lowering of mood.

Table 2 Participants with treatment-emergent SAEs and AESIs

Full size table

Suicidality was tracked throughout the study using the Columbia Suicide Severity Rating Scale (C-SSRS) at each study visit. More than 90% of participants reported suicidal ideation in their lifetime, and 17 of 46 participants (37%) in the MDMA group and 14 of 44 participants (32%) in the placebo group reported suicidal ideation at baseline. Although the number of participants who reported suicidal ideation varied throughout the visits, prevalence never exceeded baseline and was not exacerbated in the MDMA group. Serious suicidal ideation (a score of 4 or 5 on the C-SSRS) was minimal during the study and occurred almost entirely in the placebo arm (Fig. 4).

Fig. 4: Number of participants reporting the presence of suicidal ideation as measured with the C-SSRS at each visit and separated by treatment group.

C-SSRS ideation scores range from 0 (no ideation) to 5. A C-SSRS ideation score of 4 or 5 is termed 'serious ideation'. The number of participants endorsing any positive ideation (>0) is shown by the colored bars and noted in the table below the graph. The number of participants endorsing serious ideation is given in parentheses in the table.

Full size image

Discussion

Here, we demonstrate that three doses of MDMA given in conjunction with manualized therapy over the course of 18 weeks results in a significant and robust attenuation of PTSD symptoms and functional impairment as assessed using the CAPS-5 and SDS, respectively. MDMA also significantly mitigated depressive symptoms as assessed using the BDI-II. Of note, MDMA did not increase the occurrence of suicidality during the study.

These data illustrate the potential benefit of MDMA-assisted therapy for PTSD over the FDA-approved first-line pharmacotherapies sertraline and paroxetine, which have both exhibited smaller effect sizes in pivotal studies16. Previous comparison of change in CAPS score between sertraline and placebo showed effect sizes of 0.31 and 0.37 (ref. 16). Similarly, comparison of change in CAPS score between paroxetine and placebo showed effect sizes of 0.56, 0.45 and 0.09 (ref. 16). By contrast, the effect size of 0.91 demonstrated in this study between MDMA-assisted therapy and placebo with therapy was larger than that for any other previously identified PTSD pharmacotherapy16,17,18. To directly assess superiority, a head-to-head comparison of MDMA-assisted therapy with SSRIs for PTSD would be needed. Although the present study tested the effects of MDMA using a model in which both treatment groups received supportive therapy, participants who received MDMA and supportive therapy (d = 2.1) had greater improvement in PTSD change scores compared with those who received placebo with supportive therapy (d = 1.2), suggesting that MDMA enhanced the effects of supportive therapy. In clinical practice, both MDMA and supportive therapy will be components of this PTSD treatment.

Previous research on MDMA for PTSD has suggested that those with a recent history of SSRI treatment may not respond as robustly to MDMA18. Given that 65.5% of participants in the current trial have a lifetime history of SSRI use, it is difficult to separate the ramifications of long-term SSRI treatment from the effects of treatment resistance. However, there was no obvious effect of previous SSRI use on therapeutic efficacy in this trial. Similarly, although years of PTSD diagnosis or age of onset may affect treatment efficacy, no obvious relationship was seen here between duration or onset of PTSD diagnosis and treatment efficacy.

Serotonin and the serotonin transporter are of particular importance in the generation, consolidation, retrieval and reconsolidation of fear memories19,20. Reduced serotonin transporter levels (which result in greater amounts of extracellular serotonin) have been shown to predict propensity to develop PTSD21, increase fear and anxiety-related behaviors22, and induce greater amygdalar blood oxygenation level-dependent (BOLD) activity in response to fearful images23. There is extensive serotonergic innervation of the amygdala, and amygdalar serotonin levels have been shown to increase following exposure to stressful and fear-inducing stimuli24. MDMA enhances the extinction of fear memories in mice through increased expression of brain-derived neurotrophic factor in the amygdala, and human neuroimaging studies have demonstrated that MDMA is associated with attenuated amygdalar BOLD activity during presentation of negative emotional stimuli25. Together these data suggest that MDMA may exert its therapeutic effects through a well-conserved mechanism of amygdalar serotonergic function that regulates fear-based behaviors and contributes to the maintenance of PTSD. Perhaps by reopening an oxytocin-dependent critical period of neuroplasticity that typically closes after adolescence15, MDMA may facilitate the processing and release of particularly intractable, potentially developmental, fear-related memories.

It is intriguing to speculate that the pharmacological properties of MDMA, when combined with therapy, may produce a 'window of tolerance,' in which participants are able to revisit and process traumatic content without becoming overwhelmed or encumbered by hyperarousal and dissociative symptoms26. MDMA-assisted therapy may facilitate recall of negative or threatening memories with greater self-compassion27 and less PTSD-related shame and anger28. Additionally, the acute prosocial and interpersonal effects of MDMA25,29 may support the quality of the therapeutic alliance, a potentially important factor relating to PTSD treatment adherence30 and outcome31. Indeed, clinicians have suggested that "MDMA may catalyze therapeutic processing by allowing patients to stay emotionally engaged while revisiting traumatic experiences without becoming overwhelmed"32.

Given that PTSD is a strong predictor of disability in both veteran and community populations33, it is promising to note that the robust reduction in PTSD and depressive symptoms identified here is complemented by a significant improvement in SDS score (for example, work and/or school, social and family functioning). Approximately 4.7 million US veterans report a service-related disability[34](https://www.nature.com/articles/s41591-021-01336-3#ref-CR34 "Bureau of Labor and Statistics. Employment Situation of Veterans---2020. News release, 18 March 2021; https://www.bls.gov/news.release/pdf/vet.pdf

            "), costing the US government approximately $73 billion per year[35](https://www.nature.com/articles/s41591-021-01336-3#ref-CR35 "Congressional Budget Office. Possible Higher Spending Paths for Veterans' Benefits (2018);
              https://www.cbo.gov/publication/54881

            "). Identification of a PTSD treatment that could improve social and family functioning and ameliorate impairment across a broad range of environmental contexts could provide major medical cost savings, in addition to improving the quality of life for veterans and others affected by this disorder.

PTSD is a particularly persistent and incapacitating condition when expressed in conjunction with other disorders of mood and affect. In the present study, perhaps most compelling are the data indicating efficacy in participants with chronic and severe PTSD, and the associated comorbidities including childhood trauma, depression, suicidality, history of alcohol and substance use disorders, and dissociation, because these groups are all typically considered treatment resistant2,3,4,5,6. Given that more than 80% of those assigned a PTSD diagnosis have at least one comorbid disorder3, the identification of a therapy that is effective in those with complicated PTSD and dual diagnoses could greatly improve PTSD treatment. Additional studies should therefore be conducted to evaluate the safety and efficacy of MDMA-assisted therapy for PTSD in those with specific comorbidities.

Although recent research suggests that dissociative subtype PTSD is difficult to treat36, participants with the dissociative subtype who received MDMA-assisted therapy had significant symptom reduction that was at least similar to that of their counterparts with non-dissociative PTSD. Given that this covariate was significant, it warrants further study. Furthermore, given that other treatments for PTSD are not consistently effective for those with the dissociative subtype, these data, if replicated, would indicate an important novel therapeutic niche for MDMA-assisted therapy for typically hard-to-treat populations.

Importantly, there were no major safety issues reported in the MDMA arm of this study. Although abuse potential, cardiovascular risk and suicidality were recorded as AESIs, MDMA was not shown to induce or potentiate any of these conditions. In addition, although there was often a transient increase in blood pressure during MDMA sessions, this was expected based on phase 2 data and previous studies in healthy volunteers37. These data suggest that MDMA has an equivalent, if not better, safety profile compared with that of first-line SSRIs for the treatment of PTSD, which are known to carry a low risk of QT interval prolongation38.

There are several limitations to the current trial. First, due to the coronavirus disease 2019 (COVID-19) pandemic, the participant population is smaller than originally planned. However, given the power noted in this study, it is unlikely that population size was an impediment. Second, the population is relatively homogeneous and lacks racial and ethnic diversity, which should be addressed in future trials. Third, this report describes the findings of a short-term pre-specified primary outcome, 2 months after the last experimental session and 5 weeks since the final integrative therapy session; long-term follow-up data from this controlled trial will be collected to assess durability of treatment. Fourth, safety data were by necessity collected by site therapists, perhaps limiting the blinding of the data. To eliminate this effect on the primary and secondary outcome measures, all efficacy data were collected by blinded, independent raters. Last, given the subjective effects of MDMA, the blinding of participants was also challenging and possibly led to expectation effects14. However, although blinding was not formally assessed during the study, when participants were contacted to be informed of their treatment assignment at the time of study unblinding it became apparent that at least 10% had inaccurately guessed their treatment arm. Although anecdotal, at least 7 of 44 participants in the placebo group (15.9%) inaccurately believed that they had received MDMA, and at least 2 of 46 participants in the MDMA group (4.3%) inaccurately believed that they had received placebo.

We may soon be confronted with the potentially enormous economic and social repercussions of PTSD, exacerbated by the COVID-19 pandemic. Overwhelmingly high rates of psychological and mental health impairment could be with us for years to come and are likely to impart a considerable emotional and economic burden. Novel PTSD therapeutics are desperately needed, especially for those for whom comorbidities confer treatment resistance.

In summary, MDMA-assisted therapy induces rapid onset of treatment efficacy, even in those with severe PTSD, and in those with associated comorbidities including dissociative PTSD, depression, history of alcohol and substance use disorders, and childhood trauma. Not only is MDMA-assisted therapy efficacious in individuals with severe PTSD, but it may also provide improved patient safety. Compared with current first-line pharmacological and behavioral therapies, MDMA-assisted therapy has the potential to dramatically transform treatment for PTSD and should be expeditiously evaluated for clinical use.

not surveys? is that bc opinion-gathering is too much about hypothetical future actions and doesn't validate via existing present action?

I guess the reception to an artifact is inherently a survey—although it constrains the reception to the vehicle of the artifact's form

Reviewer #1 (Public Review):

Hippocampal place cells display a sequence of firing activities when the animal travels through a spatial trajectory at a behavioral time scale of seconds to tens of seconds. Interestingly, parts of the firing sequence also occur at a much shorter time scale: ~120 ms within individual cycles of theta oscillation. These so-called theta sequences are originally thought to naturally result from the phenomenon of theta phase precession. However, there is evidence that theta sequences do not always occur even when theta phase precession is present, for example, during the early experience of a novel maze. The question is then how they emerge with experience (theta sequence development). This study presents evidence that a special group of place cells, those tuned to fast-gamma oscillations, may play a key role in theta sequence development.

The authors analyzed place cells, LFPs, and theta sequences as rats traveled a circular maze in repeated laps. They found that a group of place cells were significantly tuned to a particular phase of fast-gamma (FG-cells), in contrast to others that did not show such tunning (NFG-cells). The authors then omitted FG-cells or the same number of NFG-cells, in their algorithm of theta sequence detection and found that the quality of theta sequences, quantified by a weighted correlation, was worse with the FG-cell omission, compared to that with the NFG-cell omission, during later laps, but not during early laps. What made the FG-cells special for theta sequences? The authors found that FG-cells, but not NFG-cells, displayed phase recession to slow-gamma (25 - 45 Hz) oscillations (within theta cycles) during early laps (both FG- and NFG-cells showed slow-gamma phase precession during later laps). Overall, the authors conclude that FG-cells contribute to theta sequence development through slow-gamma phase precession during early laps.

How theta sequences are formed and developed during experience is an important question, because these sequences have been implicated in several cognitive functions of place cells, including memory-guided spatial navigation. The identification of FG-cells in this study is straightforward. Evidence is also presented for the role of these cells in theta sequence development. However, given several concerns elaborated below, whether the evidence is sufficiently strong for the conclusion needs further clarification, perhaps, in future studies.

(1) The results in Figure 3 and Figure 8 seems contradictory. In Figure 8, all theta sequences displayed a seemingly significant weighted correlation (above 0) even in early laps, which was mostly due to FG-cell sequences but not NFG-cell sequences (correlation for NFG-sequences appeared below 0). However, in Figure 3H, omitting FG-cells and omitting NFG-cells did not produce significant differences in the correlation. Conversely, FG-cell and NFG-cell sequences were similar in later laps in Figure 8 (NFG-cell sequences appeared even better than FG-cell sequences), yet omitting NFG-cells produced a better correlation than omitting FG-cells. This confusion may be related to how "FG-cell-dominant sequences" were defined, which is unclear in the manuscript. Nevertheless, the different results are not easy to understand.

(2) The different contributions between FG-cells and NFG-cells to theta sequences are supposed not to be caused by their different firing properties (Figure 5). However, Figure 5D and E showed a large effect size (Cohen's D = 07, 0.8), although not significant (P = 0.09, 0.06). But the seemingly non-significant P values could be simply due to smaller N's (~20). In other parts of the manuscript, the effect sizes were comparable or even smaller (e.g. D = 0.5 in Figure 7B), but interpreted as positive results: P values were significant with large N's (~480 in Fig. 7B). Drawing a conclusion purely based on a P value while N is large often renders the conclusion only statistical, with unclear physical meaning. Although this is common in neuroscience publications, it makes more sense to at least make multiple inferences using similar sample sizes in the same study.

(3) In supplementary Figure 2 - S2, FG-cells displayed stronger theta phase precession than NFG-cells, which could be a major reason why FG-cells impacted theta sequences more than NFG cells. Although factors other than theta phase precession may contribute to or interfere with theta sequences, stronger theta phase precession itself (without the interference of other factors), by definition, can lead to stronger theta sequences.

(4) The slow-gamma phase precession of FG-cells during early laps is supposed to mediate or contribute to the emergence of theta sequences during late laps (Figure 1). The logic of this model is unclear. The slow-gamma phase precession was present in both early and late laps for FG-cells, but only present in late laps for NFG-cells. It seems more straightforward to hypothesize that the difference in theta sequences between early and later laps is due to the difference in slow-gamma phase precession of NFG cells between early and late laps. Although this is not necessarily the case, the argument presented in the manuscript is not easy to follow.

(5) There are several questions on the description of methods, which could be addressed to clarify or strengthen the conclusions.

(i) Were the identified fast- and slow-gamma episodes mutually exclusive?

(ii) Was the task novel when the data were acquired? How many days (from the 1st day of the task) were included in the analysis? When the development of the theta sequence was mentioned, did it mean the development in a novel environment, in a novel task, or purely in a sense of early laps (Lap 1, 2) on each day?

(iii) How were the animals' behavioral parameters equalized between early and later laps? For example, speed or head direction could potentially produce the differences in theta sequences.