Author response:

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

eLife assessment

The authors develop a self-returning self-avoiding polymer model of chromosome organization and show that their framework can recapitulate at the same time local density and large-scale contact structural properties observed experimentally by various technologies. The presented theoretical framework and the results are valuable for the community of modelers working on 3D genomics. The work provides solid evidence that such a framework can be used, is reliable in describing chromatin organization at multiple scales, and could represent an interesting alternative to standard molecular dynamics simulations of chromatin polymer models.

We appreciate the editor for an accurate description of the scope of the paper.

Public Reviews:

Reviewer #1 (Public Review):

Carignano et al propose an extension of the self-returning random walk (SRRW) model for chromatin to include excluded volume aspects and use it to investigate generic local and global properties of the chromosome 3D organization inside eukaryotic nuclei. In particular, they focus on chromatin volumic density, contact probability, and domain size and suggest that their framework can recapitulate several experimental observations and predict the effect of some perturbations.

We thanks the reviewer for the attention paid to the manuscript and all the relevant comments.

Strengths:

- The developed methodology is convincing and may offer an alternative - less computationally demanding - framework to investigate the single-cell and population structural properties of 3D genome organization at multiple scales.

- Compared to the previous SRRW model, it allows for investigation of the role of excluded volume locally.

Excluded volume is accounted for everywhere, not locally. We emphasized this on page 3, line 182:

“The method that we employ to remove overlaps is a low-temperature-controlled molecular dynamics simulation using a soft repulsive interaction potential between initially overlapping beads, that is terminated as soon as all overlaps have been resolved, as described in the Appendix 3.”


- They perform some experiments to compare with model predictions and show consistency between the two.

Weaknesses:

- The model is a homopolymer model and currently cannot fully account for specific mechanisms that may shape the heterogeneous, complex organization of chromosomes (TAD at specific positions, A/B compartmentalization, promoter-enhancer loops, etc.).

The SR-EV model is definitely not a homo-polymer, as it is not a regular concatenation of a single monomeric unit.

The model includes loops, which may happen in two ways: 1) As in the SRRW, branching structures emerging from the configuration backbone can be interpreted as nested loops and 2) A relatively long forward step followed by a return is a single loop. The model induces the formation of packing domains, which are not TADs, and are quantitatively in agreement with ChromSTEM experiments.

We consider convenient to add a new figure that will further clarify the structures obtained with the SR-EV model. The following paragraph and figure has been added in page 5:

“The density heterogeneity displayed by the SR-EV configurations can be analyzed in terms of the accessibility. One way to reveal this accessibility is by calculating the coordinations number (CN) for each nucleosome, using a coordination radius of 11.5 nm, along the SR-EV configuration. CN values range from 0 for an isolated nucleosome to 12 for a nucleosome immersed in a packing domain. In Figure 3 we show the SR-EV configuration showed in Figure 2, but colored according to CN. CN can be also considered as a measure to discriminate heterochromatin (red) and euchromatin (blue). Figure 3-A shows how the density inhomogeneity is coupled to different CN, with high CN represented in red and low CN represented in blue. Figure 3-B show a 50 nm thick slab obtained from the same configuration that clearly show the nucleosomes at the center of each packing domains are almost completely inaccesible, while those outside are open and accessible. It is also clear that the surface of the packing domains are characterized by nearly white nucleosomes, i.e. coordinated towards the center of the domain and open in the opposite direction.”

- By construction of their framework, the effect of excluded volume is only local and larger-scale properties for which excluded volume could be a main actor (formation of chromosome territories [Rosa & Everaers, PLoS CB 2009], bottle-brush effects due to loop extrusion [Polovnikov et al, PRX 2023], etc.) cannot be captured.

Excluded volume is considered for all nucleosomes, including overlapping beads distant along the polymer chain. Chromosome territories can be treated, but it is not in this case because we look at a single model chromosome.

- Apart from being a computationally interesting approach to generating realistic 3D chromosome organization, the method offers fewer possibilities than standard polymer models (eg, MD simulations) of chromatin (no dynamics, no specific mechanisms, etc.) with likely the same predictive power under the same hypotheses. In particular, authors often claim the superiority of their approach to describing the local chromatin compaction compared to previous polymer models without showing it or citing any relevant references that would show it.

We apologize if the text transmit an idea of superiority over other methods that was not intended. SR-EV is an alternative tool that may give a different, even complementary point of view, to standard polymer models.

- Comparisons with experiments are solid but are not quantified.

The comparisons that we have presented are quantitative. We do not have so far a way to characterize alpha or phi, a priori, for a particular system.

Impact:

Building on the presented framework in the future to incorporate TAD and compartments may offer an interesting model to study the single-cell heterogeneity of chromatin organization. But currently, in this reviewer's opinion, standard polymer modeling frameworks may offer more possibilities.

We thank the reviewer for the positive opinion on the potential of the presented method. The incorporation of TADs and compartments is left for a future evolution of the model as its complexity will make this work extremely long.

Reviewer #2 (Public Review):

Summary:

The authors introduce a simple Self Returning Excluded Volume (SR-EV) model to investigate the 3D organization of chromatin. This is a random walk with a probability to self-return accounting for the excluded volume effects. The authors use this method to study the statistical properties of chromatin organization in 3D. They compute contact probabilities, 3D distances, and packing properties of chromatin and compare them with a set of experimental data.

We thank the reviewer for the attention paid to our manuscript.

Strengths:

(1) Typically, to generate a polymer with excluded volume interactions, one needs to run long simulations with computationally expensive repulsive potentials like the WeeksChanlder-Anderson potential. However, here, instead of performing long simulations, the authors have devised a method where they can grow polymer, enabling quick generation of configurations.

(2) Authors show that the chromatin configurations generated from their models do satisfy many of the experimentally known statistical properties of chromatin. Contact probability scalings and packing properties are comparable with Chromatin Scanning Transmission Electron Microscopy (ChromSTEM)  experimental data from some of the cell types.

Weaknesses:

This can only generate broad statistical distributions. This method cannot generate sequence-dependent effects, specific TAD structures, or compartments without a prior model for the folding parameter alpha. It cannot generate a 3D distance between specific sets of genes. This is an interesting soft-matter physics study. However, the output is only as good as the alpha value one provides as input.

We proposed a model to create realistic chromatin configuration that we have contrasted with specific single cell experiments, and also reproducing ensemble average properties. 3D distances between genes can be calculated after mapping the genome to the SR-EV configuration. The future incorporation of the genome sequence will also allow us to describe TADs and A/B compartments. See added paragraph in the Discussion section:

“The incorporation of genomic character to the SR-EV model will allow us to study all individual single chromosomes properties, and also topological associated domains and A/B compartmentalization from ensemble of configurations as in HiC experiments. “

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Major:

- In the introduction and along the text, the authors are often making strong criticisms of previous works (mostly polymer simulation-based) to emphasize the need for an alternative approach or to emphasize the outcomes of their model. Most of these statements (see below) are incomplete if not wrong. I would suggest tuning down or completely removing them unless they are explicitly demonstrated (eg, by explicit quantitative comparisons). There is no need to claim any - fake - superiority over other approaches to demonstrate the usefulness of an approach. Complementarity or redundance in the approaches could also be beneficial.

We regret if we unintentionally transmitted a claim of superiority. We have made several small edits to change that.

- Line 42-43: at least there exist many works towards that direction (including polymer modeling, but also statistical modeling). For eg, see the recent review of Franck Alber.

Line removed. Citation to Franck Alber included below in the text.

- Line 54-57: Point 1 is correct but is it a fair limitation? These models can predict TADs & compartments while SR-EV no. Point 2 is wrong, it depends on the resolution of the model and computer capacity but it is not an intrinsic limitation. Point 3 is wrong, such models can predict very well single-cell properties, and again it is not an intrinsic limitation of the model. Point 4 is incorrect. The space-filling/fractal organization was an (unfortunate) picture to emphasize the typical organization of chromosomes in the early times (2009), but crumpled polymers which are a more realistic description are not space-filling (see Halverson et al, 2013).

Text involving points 1 to 4 removed. It was unnecessary and does not change the line of the paper.

- L400-402 + 409-411: in such a model, the biphasic structure may emerge from loop extrusion but also naturally from the crumpled polymer organization. Simple crumpled polymer without loop extrusion and phase separation would also produce biphasic structures.

Yes, we agree. Also SR-EV leads to biphasic structures.

- L 448-449: any data to show that existing polymer modeling would predict a strong dependency of C_p(n) on the volumic fraction (in the range studied here)?

No, I don’t know a work predicting that.

- Fig. 4:

- Large-scale structural properties (R^2(n) and C_p(n)) are not dependent on phi. Is it surprising that by construction, SR-EV only relaxes the system locally after SRRW application?

Excluded volume is considered at all length scales. However, as the decreasing C_p curves observed in theories and experiments imply, the fraction of overlap (or contacts) is more important at small separations (local) than at large separations. Yet, it was a surprise for us to observed negligible effect on phi.

- Why not make a quantitative comparison between predicted and measured C_p(n)? Or at least plotting them on the same panel.

Panels B and C are in the same scale and show a good agreement between SR-EV and experiments. However, it is not perfectly quantitative agreement. SR-EV represents the generic structure of chromatin and perfect agreement should not be expected.

- Comparison with an average C_p(n) over all the chromosomes would be better.

Possibly, but we don’t think it adds anything to the paper.

- In Figure 5,6,7 (and related text): authors often describe some parameter values that are 'closest to experiment findings'. Can the authors quantify/justify this? The various 'closest' parameters are different. Can the authors comment?

The folding parameter and average volume fraction are chose so that the agreement is best with the displayed experimental system, different cell for each case.

- Figure 5: why not show the experimental distribution from Ou et al?

- Figure 6 & 7: experimental results. Can the authors show images from their own experiments? Can they show that cohesion/RAD21 is really depleted after auxin treatment?

It is currently under review in a different journal.

- In the Discussion, a fair discussion on the limitations of the methods (dynamics, etc) is missing.

Minor

- Line 34-36: the logical relationship between this sentence and the ones before and after is very unclear.

- Along the text, authors use the term 'connectivity' to describe 3D (Hi-C) contacts between different regions of the same chromosome/polymer. This is misleading as connectivity in polymer physics describes the connection along the polymer and not in the 3D space.

No. I don’t think we used connectivity in that sense. We agree with your statement on the use of connectivity in polymer physics, and is what we always had in mind for this model.

- Line 92: typo.

- On the SR-EV method: does the relaxation process create local knots in the structure?

We have not checked for knots.

- Table 1: the good correspondence with linker length is remarkable but likely 'fortunate', other chosen resolutions would have led to other results. Moreover, the model cannot account for the fine structure of chromatin fiber. Can the authors comment on that?

Fortunate to the extent that we sample the model parameter to overall catch the structure of chromatin.

- Line 211: 'without the need of imposing any parameter': alpha is a parameter, no?

Correct. Phrase deleted.

- L267-269 & 450-451: actually in Liu & Dekker, they do observe an effect on Hi-C map (C_p(n)), weak but significant and not negligible.

Our statements read ‘minimal’ and ‘relatively insensitive’. It is observed, but very small.

- L283-286: This is a perspective statement that should be in the discussion.

Moved to the Discussion, as suggested.

- L239-241: The authors seem to emphasize some contradictions with recent results on phase separation. This is unclear and should be relocated to discussion.

We just pointed out recent experiments, as stated. No intention to generate a discussion with any of them.

- L311-313: Unclear statement.

- L316-325: This is not results but discussion/speculation.

Moved to Discussion

- Along the text: 'promotor'-> 'promoter'. 

- Corrected.

- L364: explain more in detail PWS microscopy.

Reviewer #2 (Recommendations For The Authors):

Even though there are claims about nucleosome-resolution chromatin polymer, it is not clear that this work can generate structures with known nucleosome-resolution features. Nucleosome-level structure is much beyond a random walk with excluded volume and is driven by specific interactions. The authors should clarify this.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Yang, Hu et al. examined the molecular mechanisms underlying astrocyte activation and its implications for multiple sclerosis. This study shows that the glycolytic enzyme PKM2 relocates to astrocyte nuclei upon activation in EAE mice. Inhibiting PKM2's nuclear import reduces astrocyte activation, as evidenced by decreased proliferation, glycolysis, and inflammatory cytokine release. Crucially, the study identifies TRIM21 as pivotal in regulating PKM2 nuclear import via ubiquitination. TRIM21 interacts with PKM2, promoting its nuclear translocation and enhancing its activity, affecting multiple signaling pathways. Confirmatory analyses using single-cell RNA sequencing and immunofluorescence demonstrate TRIM21 upregulation in EAE astrocytes. Modulating TRIM21 expression in primary astrocytes impacts PKM2-dependent glycolysis and proliferation. In vivo experiments targeting this mechanism effectively mitigate disease severity, CNS inflammation, and demyelination in EAE.

The authors supported their claims with various experimental approaches, however, some results should be supported with higher-quality images clearly depicting the conclusions and additional quantitative analyses of Western blots.

Thanks for the reviewer’s comments. We agree with the reviewer and have added higher magnification images, for example Fig.2A to better visualize the localization of PKM2 in DASA-treated conditions, and Fig. 3A and Fig.3B to better visualize the pSTAT3 and pp65. Moreover, we have added quantitative analyses of Western blots for some key experiments, for example quantitative results for Fig.2D is added in Fig.S3 to show the change of PKM2 and p-c-myc in DASA-58-treated conditions and quantitative results for Fig. 3D are added in Fig.S4B and S4C to show the change of nuclear and cytoplasmic PKM2, STAT3 and NF-κB in different conditions.

Strength:

This study presents a comprehensive investigation into the function and molecular mechanism of metabolic reprogramming in the activation of astrocytes, a critical aspect of various neurological diseases, especially multiple sclerosis. The study uses the EAE mouse model, which closely resembles MS. This makes the results relevant and potentially translational. The research clarifies how TRIM21 regulates the nuclear import of PKM2 through ubiquitination by integrating advanced techniques. Targeting this axis may have therapeutic benefits since lentiviral vector-mediated knockdown of TRIM21 in vivo significantly reduces disease severity, CNS inflammation, and demyelination in EAE animals.

We thank the reviewer for their positive and constructive comments on the manuscript.

Weaknesses:

The authors reported that PKM2 levels are elevated in the nucleus of astrocytes at different EAE phases compared to cytoplasmic localization. However, Figure 1 also shows elevated cytoplasmic expression of PKM2. The authors should clarify the nuclear localization of PKM2 by providing zoomed-in images. An explanation for the increased cytoplasmic PKM2 expression should provided. Similarly, while PKM2 translocation is inhibited by DASA-58, in addition to its nuclear localization, a decrease in the cytoplasmic localization of PKM2 is also observed. This situation brings to mind the possibility of a degradation mechanism being involved when its nuclear translocation of PKM2 is inhibited.

According to the results of immunofluorescence staining of PKM2 in spinal cord of EAE mice and in cultured primary astrocytes, in addition to the observation of PKM2 nuclear translocation in EAE conditions, we showed an elevated expression of PKM2 in astrocytes, including the cytoplasmic and nuclear expression. In neurological diseases, various studies showed consistent results, for example, following spinal cord injury (SCI), not only the upregulated expressing of PKM2 but also nuclear translocation was observed in astrocytes (Zhang et al., 2015). In EAE conditions, CNS inflammation is elevated and several proinflammatory cytokines and chemokines might contribute to the upregulated expression of PKM2 in astrocytes. We have tested TNFα and IL-1β, which are recognized to play important roles in EAE and MS (Lin and Edelson, 2017, Wheeler et al., 2020), and results from western blots showed the increased expression of PKM2 upon stimulation with TNFα and IL-1β (Author response image 1). Moreover, according to the reviewer’s suggestions, we have added zoomed-in images for figure 2A.

Additionally, the reviewer has noted the decrease in the cytoplasmic PKM2 level, degradation-related mechanism and other mechanisms might be involved in this process.

Author response image 1.

Upregulated expression of PKM2 in astrocytes following stimulation with TNF-α and IL-1β. Primary astrocytes were stimulated with TNF-α and IL-1β (50 ng/mL) for 48 h and western blotting analysis were performed.

In Figure 3D, the authors claim that PKM2 expression causes nuclear retention of STAT3, p65, and p50, and inhibiting PKM2 localization with DASA-58 suppresses this retention. The western blot results for the MOG-stimulated group show high levels of STAT3, p50, and p65 in nuclear localization. However, in the MOG and DASA-58 treated group, one would expect high levels of p50, p65, and STAT3 proteins in the cytoplasm, while their levels decrease in the nucleus. These western blot results could be expanded. Additionally, intensity quantification for these results would be beneficial to see the statistical difference in their expressions, especially to observe the nuclear localization of PKM2.

We agree with the reviewer’s comments and we have incorporated the quantification of STAT3，p50 and p65 for Fig.3D and Fig.S4B and Fig.S4C. Nevertheless, given that DASA-58 did not trigger a notable increase in the cytoplasmic level of PKM2, we did not detect an upregulation of STAT3, p50, or p65 in the cytoplasm of the MOG and DASA-58-treated groups. With the quantification results, it is more obvious to see the changes of these proteins in different conditions.

The discrepancy between Figure 7A and its explaining text is confusing. The expectation from the knocking down of TRIM21 is the amelioration of activated astrocytes, leading to a decrease in inflammation and the disease state. The presented results support these expectations, while the images showing demyelination in EAE animals are not highly supportive. Clearly labeling demyelinated areas would enhance readers' understanding of the important impact of TRIM21 knockdown on reducing the disease severity.

Thank you for pointing this out. We sincerely apologize for our carelessness. Based on your comments, we have made the corrections in the manuscript. As there is indeed a statistical difference in the mean clinical scores between shTRIM21-treated group and shVec group, we have accordingly revised the sentence for Figure 7A to state, “At the end time point at day 22 p.i., shTRIM21-treated group showed reduced disease scores compared to control groups (Fig. 7A).” .

Additionally, we have added the whole image of the spinal cord for MBP in Author Response image 2. Moreover, we have labelled the demyelinated areas to facilitate readers’ understanding.

Author response image 2.

MBP staining of the whole spinal cord in EAE mice from shVec and shTRIM21 group. Scale bar: 100 μm. Demyelinated areas are marked with dashed lines.

Reviewer #2 (Public Review):

This study significantly advances our understanding of the metabolic reprogramming underlying astrocyte activation in neurological diseases such as multiple sclerosis. By employing an experimental autoimmune encephalomyelitis (EAE) mouse model, the authors discovered a notable nuclear translocation of PKM2, a key enzyme in glycolysis, within astrocytes.

Preventing this nuclear import via DASA 58 substantially attenuated primary astrocyte activation, characterized by reduced proliferation, glycolysis, and inflammatory cytokine secretion.<br /> Moreover, the authors uncovered a novel regulatory mechanism involving the ubiquitin ligase TRIM21, which mediates PKM2 nuclear import. TRIM21 interaction with PKM2 facilitated its nuclear translocation, enhancing its activity in phosphorylating STAT3, NFκB, and c-myc. Single-cell RNA sequencing and immunofluorescence staining further supported the upregulation of TRIM21 expression in astrocytes during EAE.

Manipulating this pathway, either through TRIM21 overexpression in primary astrocytes or knockdown of TRIM21 in vivo, had profound effects on disease severity, CNS inflammation, and demyelination in EAE mice. This comprehensive study provides invaluable insights into the pathological role of nuclear PKM2 and the ubiquitination-mediated regulatory mechanism driving astrocyte activation.

The author's use of diverse techniques, including single-cell RNA sequencing, immunofluorescence staining, and lentiviral vector knockdown, underscores the robustness of their findings and interpretations. Ultimately, targeting this PKM2-TRIM21 axis emerges as a promising therapeutic strategy for neurological diseases involving astrocyte dysfunction.

While the strengths of this piece of work are undeniable, some concerns could be addressed to refine its impact and clarity further; as outlined in the recommendations for the authors.

Thanks for the reviewer’s comment and positive evaluation of our present work. We have further answered each question in recommendations section.

Reviewer #3 (Public Review):

Summary:

Pyruvate kinase M2 (PKM2) is a rate-limiting enzyme in glycolysis and its translocation to the nucleus in astrocytes in various nervous system pathologies has been associated with a metabolic switch to glycolysis which is a sign of reactive astrogliosis. The authors investigated whether this occurs in experimental autoimmune encephalomyelitis (EAA), an animal model of multiple sclerosis (MS). They show that in EAA, PKM2 is ubiquitinated by TRIM21 and transferred to the nucleus in astrocytes. Inhibition of TRIM21-PKM2 axis efficiently blocks reactive gliosis and partially alleviates symptoms of EAA. Authors conclude that this axis can be a potential new therapeutic target in the treatment of MS.

Strengths:

The study is well-designed, controls are appropriate and a comprehensive battery of experiments has been successfully performed. Results of in vitro assays, single-cell RNA sequencing, immunoprecipitation, RNA interference, molecular docking, and in vivo modeling etc. complement and support each other.

Weaknesses:

Though EAA is a valid model of MS, a proposed new therapeutic strategy based on this study needs to have support from human studies.

We agree that although we have clarified the therapeutic potential of targeting TRIM21 or PKM2 in the treatment of EAE, a mouse model of MS, the application in human studies warrants further studies. While considering the use of TRIM21 as a target for treating multiple sclerosis in clinical trials, several issues need to be addressed to ensure the safety, efficacy and feasibility. One such aspect is the development of drug that specifically target TRIM21 in brain, capable of crossing the blood-brain barrier and have minimal off-target effects. The translation of preclinical finding into clinical trials poses a significant challenge. To provide evidence for the similarities between the EAE model and multiple sclerosis, we have screened GEO databases (Author response image 3). In GSE214334 which analyzed transcriptional profiles of normal-appearing white matter from non-MS and different subtypes of disease (RRMS, SPMS and PPMS). Although no statistical difference was observed among different groups, the TRIM21 expression has tendency to increase in SPMS (secondary progressive MS) and PPMS (primary progressive MS) patients. In GSE83670, astrocytes from 3 control white matter and 4 multiple sclerosis normal appearing white matter (NAWM) were analyzed. TRIM21 mRNA expression is higher in MS group (78.73 ± 10.44) compared to control group (46.67 ± 24.15). Although these two GEO databases did not yield statistically significant differences, TRIM21 expression appears to be elevated in the white matter of MS patients compared to controls.

To address this limitation, we have incorporated the following statement in the discussion section: “However, whether TRIM21-PKM2 could potentially serve as therapeutic targets in multiple sclerosis warrants further studies.”

Author response image 3.

TRIM21 expression in control and MS patients based on published GEO database. (A) The expression of TRIM21 in normal-appearing white matter in non-MS (Ctl) and different clinical subtypes of MS (RRMS, SPMS, PPMS) based on GSE214334 (one-way ANOVA). (B) The expression of TRIM21 from multiple sclerosis normal appearing white matter (NAWM) and control WM based on GSE83670. RRMS, relapsing--remitting MS; SPMS, secondary progressive MS; PPMS, primary progressive MS (unpaired Student's t test). Data are represented as the means ± SEM.

Reviewer #4 (Public Review):

Summary:

The authors report the role of the Pyruvate Kinase M2 (PKM2) enzyme nuclear translocation as fundamental in the activation of astrocytes in a model of autoimmune encephalitis (EAE). They show that astrocytes, activated through culturing in EAE splenocytes medium, increase their nuclear PKM2 with consequent activation of NFkB and STAT3 pathways. Prevention of PKM2 nuclear translocation decreases astrocyte counteracts this activation. The authors found that the E3 ubiquitin ligase TRIM21 interacts with PKM2 and promotes its nuclear translocation. In vivo, either silencing of TRIM21 or inhibition of PKM2 nuclear translocation ameliorates the severity of the disease in the EAE model.

Strengths:

This work contributes to the knowledge of the complex action of the PKM2 enzyme in the context of an autoimmune-neurological disease, highlighting its nuclear role and a novel partner, TRIM21, and thus adding a novel rationale for therapeutic targeting.

Weaknesses:

Despite the relevance of the work and its goals, some of the conclusions drawn would require more thorough proof:

I believe that the major weakness is the fact that TRIM21 is known to have per se many roles in autoimmune and immune pathways and some of the effects observed might be due to a PKM2-independent action. Some of the experiments to link the two proteins, besides their interaction, do not completely clarify the issue. On top of that, the in vivo experiments address the role of TRIM21 and the nuclear localisation of PKM2 independently, thus leaving the matter unsolved.

We agree that TRIM21 has multifunctional roles and only some of their effects are due to PKM2-independent action. It is obvious that TRIM21 functions as ubiquitin ligases and its substrate are various. Here we identify PKM2 as one of its interacting proteins and our focus is the relationship between TRIM21 and the nuclear translocation PKM2, we have used diverse experiments to clarify their relationships, for example immunoprecipitation, western blotting, immunofluorescence, cyto-nuclear protein extraction. These aforementioned experiments are key points of our studies. From the results of in vitro experiments, targeting either TRIM21 or PKM2 might be potential targets for EAE treatment. Expectedly, from in vivo experiments, either targeting TRIM21 or PKM2 nuclear transport ameliorated EAE. In order to test the relationship of TRIM21 and PKM2 nuclear transport in vivo, we have stained PKM2 in shVec and shTRIM21-treated mice. Expectedly, knocking down TRIM21 led to a decrease in the nuclear staining of PKM2 in spinal cord astrocytes in EAE models (Figure S7A). This observation underscores that the therapeutic potential of inhibiting TRIM21 in astrocytes in vivo might be partially due to its role in triggering the reduced nuclear translocation of PKM2.

Some experimental settings are not described to a level that is necessary to fully understand the data, especially for a non-expert audience: e.g. the EAE model and MOG treatment; action and reference of the different nuclear import inhibitors; use of splenocyte culture medium and the possible effect of non-EAE splenocytes.

According to the reviewer’s suggestions, we have added more detailed descriptions in the materials and methods section, for example, the use of splenocytes culture medium, mass spectrometry, HE and LFB staining have been added. More details are incorporated in the part for “EAE induction and isolation and culture of primary astrocytes”. Moreover, the reference of DASA-58 in vitro and TEPP-46 in vivo as inhibitors of PKM2 nuclear transport were added.

The statement that PKM2 is a substrate of TRIM21 ubiquitin ligase activity is an overinterpretation. There is no evidence that this interaction results in ubiquitin modification of PKM2; the ubiquitination experiment is minimal and is not performed in conditions that would allow us to see ubiquitination of PKM2 (e.g. denaturing conditions, reciprocal pull-down, catalytically inactive TRIM21, etc.).

To prevent the misunderstanding, we have revised certain statements in the manuscript. In the updated version, the description is as follows: Hereby, we recognized PKM2 as an interacting protein of TRIM21, and further studies are required to determine if it is a substrate of E3 ligase TRIM21.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

General recommendations:

- The whole manuscript needs language editing.

We appreciate the comments of the reviewers. We have improved the writing of the manuscript. All modifications are underlined.

- Details of many experiments are not given in the materials and methods.

According to the reviewer’s suggestions, we have added more details for experiments in the materials and methods. For example, “Splenocyte isolation and supernatant of MOG35-55-stimulated-splenocytes”, “mass spectrometry”, “Hematoxylin-Eosin (HE) and Luxol Fast Blue (LFB) staining” were added in the section of Materials and Methods. More detailed information is given for EAE induction and isolation and culture of primary astrocytes.

- Line properties in graphics should be corrected, some lines in box plots and error bars are very weak and hardly visible. Statistical tests should be included in figure legends as well. Statistical differences should be mentioned for control vs DASA-58 (alone) in all related figures.

We have revised the figures to enhance their visibility by thickening the lines and error bars. In accordance with the reviewer’s suggestions, we have incorporated statistical tests in figure legends. Moreover, statistical analysis has been made among all groups, if there is no asterisk indicated in the figure legend and figure panels, it means there is no statistical difference between the control vs DASA-58 groups. For most of the experiments conducted in our studies, including lactate production, glucose consumption, the EdU analysis and CCK8 analysis, the change of STAT3 and NF-κB pathways, no statistical difference was observed between the control and DASA-58 group. The reason might be due to that in unstimulated astrocytes, the expression of PKM2 is low and nuclear translocation of PKM2 are few, which may explain why DASA-58 did not exert the anticipated effect. Thus, in our experiments, we have used MOGsup to stimulate astrocytes, enabling us to observe the impact of DASA-58 on the astrocyte proliferation and glycolysis in this condition.

- Scale bars, arrows, and labeling in the images are not visible.

We have improved the images according to the reviewer’s suggestions. The scale bars, arrows are made thicker and labeling are larger. The updated figures are visible.

- Quantitative analysis of all western blot results and their statistics could be provided in every image and for every protein.

For western blotting results which are further processed with quantitative analysis, for example, Fig.2D, fig. 5G, Fig. 6A and 6B, Fig. S4, we have added their statistics in the raw data sections. The other western blot results, for example, IP analysis, which are used to analyze protein-protein binding are not further processed with quantitative analysis.

- Proteins that are used for normalizations in western blots should be stated in the text.

We have added description of proteins that are used for normalization in western blots in figure legends. Moreover, in figure panels, proteins used for normalization are indicated. Globally, whole protein level is normalized to protein level of β-actin. For nuclear and cytoplasmic proteins, nuclear protein is normalized to the expression of lamin, cytoplasmic protein is normalized to the expression of tubulin. 

- The manuscript investigates the role of TRIM21 in the nuclear localization of PKM2 in astrocytes in EAE mice, however almost no information is given about TRIM21 in the introduction. Extra information is given for PKM2, yet can be concisely explained.

We have added a paragraph that describes the information of TRIM21 in the introduction section. The description is as follows: “TRIM21 belongs to the TRIM protein family which possess the E3 ubiquitin ligase activity. In addition to its well-recognized function in antiviral responses, emerging evidences have documented the multifaceted role of TRIM21 in cell cycle regulation, inflammation and metabolism (Chen et al., 2022). Nevertheless, the precise mechanisms underlying the involvement of TRIM21 in CNS diseases remain largely unexplored.”

- "As such, deciphering glycolysis-dominant metabolic switch in astrocytes is the basis for understanding astrogliosis and the development of neurological diseases such as multiple sclerosis." The sentence could be supported by references.

To support this sentence, we have added the following references:

(1) Xiong XY, Tang Y, Yang QW. Metabolic changes favor the activity and heterogeneity of reactive astrocytes. Trends in endocrinology and metabolism: TEM 2022;33(6):390-400.

(2) das Neves SP, Sousa JC, Magalhães R, Gao F, Coppola G, Mériaux S, et al. Astrocytes Undergo Metabolic Reprogramming in the Multiple Sclerosis Animal Model. Cells 2023;12(20):2484.

Figure 1/Result 1:

- Figure 1A-B: Quality of the images should be improved.

According to the reviewer’s suggestion, we have improved the quality of the image, images with higher resolution were added in figure 1A and figure 1B.

- Control images of Figure 1B are not satisfying. GFAP staining is very dim. Images from control cells should be renewed.

As mentioned by the reviewer’s, we have renewed the control images and added the DAPI staining figures for all groups. Compared with MOGsup stimulated astrocytes, the control cells are not in activated state and GFAP are relatively low.

- Labelings on the images are not sufficient, arrows and scale bars are not visible.

We have improved the images including labels, arrows and scale bars in all figures.

- How splenocytes were obtained from MOG induced mice were not given in the material and methods section. Thus, it should be clearly stated how splenocyte supernatant is generated (treatment details).

We have added the detailed information relating to splenocyte isolation and splenocyte supernatant entitled “Splenocyte isolation and supernatant of MOG35-55-stimulated-splenocytes” in the section of Materials and methods. “Splenocytes were isolated from EAE mice 15 d (disease onset) after MOG35-55 immunization. Briefly, spleen cells were suspended in RPMI-1640 medium containing 10% FBS. Splenocytes were plated in 12-well plates at 1x106 cells/well containing 50 μg/mL MOG35-55 and cultured at 37°C in 5% CO2. After stimulation for 60 h, cell suspension was centrifuged at 3000 rpm for 5 min and supernatants were collected. For the culture of MOGsup-stimulated astrocytes, astrocytes were grown in medium containing 70% DMEM supplemented with 10% FBS and 30% supernatant from MOG35-55-stimulated-splenocytes.”

- For general astrocyte morphology: authors showed the cells are GFAP+ astrocytes. It is surprising that these cells do not bear classical astrocyte morphology in cell culture. How long do you culture astrocytes before treatment? How do you explain their morphological difference?

Astrocytes were cultured for 2 to 3 weeks which correspond to 2-3 passages before treatment. There are several possible reasons for the morphological differences observed between GFAP+ astrocytes and their classical morphology. Firstly, the cell density. In low-density culture just as shown in Figure 1B, we have observed that astrocytes adopt a more flattened morphology. In high-density cultures, they adopt a stellate shape. Moreover, variations in culture conditions, such as the use of different fetal bovine serum, can also influence the morphology of astrocytes. In addition, the mechanical injury induced by the isolation procedures for astrocytes might contribute to variations in their morphology during in vitro cultivation. In summary, the morphological differences observed in GFAP+ astrocytes in cell culture likely result from a combination of culture conditions, cell density, and mechanical injury occured during astrocyte isolation etc.

- Additional verification of reactive astrocytes could be performed by different reactive astrocyte markers, such as GLAST, Sox9, S100ß. Thus, quantitative analysis of activated astrocytes can be done by counting DAPI vs GLAST, Sox9 or S100ß positive cells.

We really agree with the reviewer that there are other markers of reactive astrocytes such as GLAST, sox9 and S100β. However, numerous evidences support that GFAP is the most commonly used reactive astrocyte markers. Most of the cases, reactive astrocytes undergo GFAP overexpression. GFAP is one the most consistently induced gene in transcriptomic datasets of reactive astrocytes, confirming its usefulness as a reactive marker (Escartin et al., 2019). Thus, we have used GFAP as the marker of astrocyte activation in our study.

- How you performed quantifications for Figures 1C and 1D should be clearly explained, details are not given.

Quantification for Figure 1C and 1D were added in the figure legend. In general, Mean fluorescence intensity of PKM2 in different groups of (B) was calculated by ImageJ. The number of nuclear PKM2 was quantified by Image-Pro Plus software manually (eg. nuclear or cytoplasmic based on DAPI blue staining). The proportion of nuclear P KM2 is determined by normalizing the count of nuclear PKM2 to the count of nuclear DAPI, which represents the number of cell nuclei.

- "Together, these data demonstrated the nuclear translocation of PKM2 in astrocytes from EAE mice." Here the usage of "suggests" instead of "demonstrated".

Based on the reviewer's suggestion, we have revised the use of "demonstrated" to "suggest" in this sentence.

Result 2 and 3:

- In the literature, DASA-58 is shown to be the activator of PKM2 (https://www.nature.com/articles/nchembio.1060, https://doi.org/10.1016/j.cmet.2019.10.015).

- Providing references for the inhibitory use of DASA-58 for PKM2 would be appreciated.

DASA-58 is referred to as “PKM2 activator” due to its ability to enforce the tetramerization of PKM2, enhancing the enzymatic ability of PKM2 to catalyze PEP to pyruvate conversion. However, the enforced conversion of tetramerization of PKM2 inhibited the dimer form of PKM2, thereby inhibiting its nuclear translocation. For this reason, DASA-58 is also used as the inhibitor of nuclear translocation of PKM2. In primary BMDMs, LPS induced nuclear PKM2. However, driving PKM2 into tetramers using DASA-58 and TEPP-46 inhibited LPS-induced PKM2 nuclear translocation (Palsson-McDermott et al., 2015). Consistently, FSTL1 induced PKM2 nuclear translocation was inhibited by DASA-58 in BMDMs (Rao et al., 2022). Accordingly, we have added these references in the manuscript.

- Western blot results and statistics for PKM2 should be quantitatively given for all groups.

According to the reviewer’s suggestions, we have added the quantification of PKM2 for western blots in figure 2 and figure 3. Quantification of PKM2 in figure 2D is added in Fig S3. Quantification of PKM2 in figure 3D is added in Fig.S4B and Fig. S4C.

- Figure 3A-B: staining method/details are not mentioned in materials and methods.

Staining methods is in the paragraph entitled “Immunofluorescence” in the section of materials and methods. The descriptions are as follows:

For cell immunochemistry, cells cultured on glass coverslips were fixed with 4% PFA for 10 min at RT, followed by permeabilization with 0.3% Triton X-100. Non-specific binding was blocked with buffer containing 3% BSA for 30 min at RT. Briefly, samples were then incubated with primary antibodies and secondary antibodies. DAPI was used to stain the nuclei. Tissues and cells were observed and images were acquired using an EVOS FL Auto 2 Cell image system (Invitrogen). The fluorescence intensity was measured by ImageJ.

- In Figure 3A, in only DASA-58 treated cells, it looks like GFAP staining is decreased. It would be better to include MFI analysis for GFAP in the supplementary information.

We have added the MFI analysis for GFAP in Figure 3A in Fig.S4A. GFAP expression is decreased after DASA-58 treatment (in both control and MOGsup condition), the reason might be due to the effect of DASA-58 on inhibition of PKM2 nuclear transport, which subsequently suppress the activation of astrocytes, leading to the decreased expression of GFAP.

Result 4

- Detailed explanation of the mass spectrometry and IP experiments should be given in materials and methods. What are the conditions of the cells? Which groups were analyzed? Are they only MOG stimulated, MOG-DASA-58 treated, or only primary astrocytes without any treatment? The results should be interpreted according to the experimental group that has been analyzed.

We have added the detailed information relating to mass spectrometry and immunoprecipitation in the materials and methods. In general, two groups of cells were subjected to mass spectrometry analysis, primary astrocytes without any treatment and MOGsup-stimulated primary astrocytes. These two groups were immunoprecipitated with anti-PKM2 antibody. Moreover, in the manuscript, we have revised the sentence concerning the description of mass spectrometry. The description is as follows: “To illustrate underlying mechanism accounting for nuclear translocation of PKM2 in astrocytes, we sought to identify PKM2-interacting proteins. Here, unstimulated and MOGsup-stimulated primary astrocytes were subjected to PKM2 immunoprecipitation, followed by mass spectrometry”. Furthermore, the description of these two groups of cells were added in the figure legend of Fig.4.

Result 5:

- For the reader, it would be better to start this part by explaining the role of TRIM21 in cells by referring to the literature.

We agreed with the reviewer that beginning this part by explaining the role of TRIM21 would be better. Accordingly, we have added the following descriptions at the beginning of this part: “TRIM21 is a multifunctional E3 ubiquitin ligase that plays a crucial role in orchestrating diverse biological processes, including cell proliferation, antiviral responses, cell metabolism and inflammatory processes (Chen X. et al., 2022).” The relevant literature has been included: Chen X, Cao M, Wang P, Chu S, Li M, Hou P, et al. The emerging roles of TRIM21 in coordinating cancer metabolism, immunity and cancer treatment. Front Immunol 2022;13:968755.

- The source and the state of the cells (control vs MOG induced) should be stated (Figure 5A).

In figure 5A to 5D, single-cell RNA-seq were performed from CNS tissues of naive and different phases of EAE mice (peak and chronic). We have added this detailed information in the figure legend of Figure 5.

- Figure 5D can be placed after 5A. Data in Figure 5A is probably from naive animals, if so, it should be stated in the legend where A is explained. The group details of the data shown in Figure 5 should be clearly stated.

According to the reviewer’s suggestions, we have placed 5D after 5A. Single-cell RNA seq analysis were performed from CNS tissues of naïve mice and EAE mice. This information is stated in the legend of Figure 5A-D. “Single-cell RNA-seq profiles from naive and EAE mice (peak and chronic phase) CNS tissues. Naive (n=2); peak (dpi 14–24, n=3); chronic (dpi 21–26, n=2).”

- Immunofluorescence images should be replaced with better quality images, in control images, stainings are not visible.

We have replaced with better quality images in figure 5H and in control images, the staining is now visible.

Result 6:

- Experimental procedures should be given in detail in materials and methods.

We have revised the section of materials and methods, and more details are added. Detailed information was added for astrocyte isolation, immunoprecipitation. Moreover, mass spectrometry, Hematoxylin-Eosin (HE) and Luxol Fast Blue (LFB) staining, Splenocyte isolation and supernatant of MOG35-55-stimulated-splenocytes were added in materials and methods.

Result 7:

- In Figure 7A, the mean clinical score seems significantly reduced in the shTRIM21-treated group, although it is explained in the result text that it is not significant. Explain to us the difference between Figure 7A and the explaining text?

Thank you for pointing this out. We sincerely apologize for our carelessness. Based on your comments, we have made the corrections in the manuscript. As there is indeed a statistical difference in the mean clinical scores between shTRIM21-treated group and shVec group, we have accordingly revised the sentence for Figure 7A to state, “At the end time point at day 22 p.i., shTRIM21-treated group showed reduced disease scores compared to control groups (Fig. 7A).” .

- The staining methods for luxury fast blue and HE are not given in materials and methods.

According to the reviewer’s comments, we have added the staining methods for HE and LFB in materials and methods.

- In Figure 7E, authors claim that MBP staining is low in an image, however the image covers approximately 500 um area. One would like to see the demyelinated areas in dashed lines, and also the whole area of the spinal cord sections.

In Author response image 2, we have added the images for MBP staining of the whole area of spinal cord sections. Demyelinated areas are marked with dashed lines.

- "TEPP-46 is an allosteric activator that blocks the nuclear translocation of PKM2 by promoting its tetramerization." should be supported by references.

We have added two references for this sentence. Anastasiou D et al. showed that TEPP-46 acts as an activator by stabilizing subunit interactions and promoting tetramer formation of PKM2. Angiari S et al. showed that TEPP-46 prevented the nuclear transport of PKM2 by promoting its tetramerization in T cells.

These two references are added:

Angiari S, Runtsch MC, Sutton CE, Palsson-McDermott EM, Kelly B, Rana N, et al. Pharmacological Activation of Pyruvate Kinase M2 Inhibits CD4(+) T Cell Pathogenicity and Suppresses Autoimmunity. Cell metabolism 2020;31(2):391-405.e8.

Anastasiou D, Yu Y, Israelsen WJ, Jiang JK, Boxer MB, Hong BS, et al. Pyruvate kinase M2 activators promote tetramer formation and suppress tumorigenesis. Nature chemical biology 2012;8(10):839-47.

- Could you explain what the prevention stage is?

The term “prevention stage” was used to describe the administration of TEPP-46 before disease onset. To be more accurate, we have revised the phrase from “prevention stage” to “preventive treatment” as described in other references. For example, Ferrara et al. (Ferrara et al., 2020) used “preventive” and “preventive treatment” to mean administration before disease onset.

The revised sentences are as follows: “To test the effect of TEPP-46 on the development of EAE, the “preventive treatment” (i.e, administration before disease onset) was administered. Intraperitoneal treatment with TEPP-46 at a dosage of 50 mg/kg every other day from day 0 to day 8 post-immunization with MOG35-55 resulted in decreased disease severity (Fig. S8A).”

- In in vitro experiments, authors used DASA-58, and in vivo they used TEPP-46. What might be the reason that DASA-58 is not applied in vivo?

The effects of DASA-58 and TEPP-46 in promoting PKM2 tetramerization have been tested in vitro and has been documented. Based on in vitro absorption, distribution, metabolism and excretion profiling studies, Anastasiou et al. predicted that TEPP-46 had better in vivo drug exposure compared to DASA-58. Moreover, TEPP-46, but not DASA-58, is pharmacokinetically validated in vivo (Anastasiou et al., 2012). Thus, we used TEPP-46 for in vivo studies.

- Authors claim that TEPP-46 activates PKM2 and leads it its nuclear translocation, however, they did not verify PKM2 expression in the nucleus.

To support that TEPP-46 exerts effects in inhibiting PKM2 nuclear translocation both in vivo and in vitro, we have performed western blotting analysis and immunofluorescence staining. In vitro, TEPP-46 administration inhibited the MOGsup-induced PKM2 nuclear translocation, which exerts similar effects as DASA-58 (Author response image 4). The in vivo effects of TEPP-46 was analyzed by co-immunostaining of PKM2 and GFAP. The results showed reduced nuclear staining of PKM2 in spinal cord astrocytes in TEPP-46-treated EAE mice compared with control EAE mice (Figure S7B).

Author response image 4.

TEPP-46 inhibited the nuclear transport of PKM2 in primary astrocytes. Nuclear-cytoplasmic protein extraction analysis showed the nuclear and cytoplasmic changes of PKM2 in TEPP-46 treated astrocytes and MOGsup-stimulated astrocytes. Primary astrocytes were pretreated with 50 μM TEPP-46 for 30 min and stimulated with MOGsup for 24 h.

Supplementary Figure 3:

- In Figure 3D, merge should be stated on top of the merged images, it is confusing to the reader.

According to the reviewer’s comments, we have added merge on top of the merged images.

Discussion:

All results should be discussed in detail by interpreting them according to the literature.

We have further discussed the results in the discussion n section. Firstly, we added a paragraph describing the role of nuclear translocation of PKM2 in diverse CNS diseases. Moreover, a paragraph discussing the nuclear function of PKM2 as a protein kinase or transcriptional co-activator was added. Now the discussion section is more comprehensive, which nearly discuss all the results by interpreting them according to the literature in detail.

Reviewer #2 (Recommendations For The Authors):

The authors could address the following points:

(1) In Figure 1A, the authors present immunofluorescence staining of PKM2 in both control mice and MOG35-725 55-induced EAE mice across different stages of disease progression: onset, peak, and chronic stages. Observing the representative images suggests a notable increase in PKM2 levels, particularly within the nucleus of MOG35-725 55-induced EAE mice. However, to provide a more comprehensive analysis, it would be beneficial for the authors to include statistical data, such as average intensities {plus minus} standard deviation (SD), along with the nuclear PKM2 ratio, akin to the presentation for cultured primary astrocytes in vitro in panels B-D. Additionally, the authors should clearly specify the number of technical repeats and the total number of animals utilized for these data sets to ensure transparency and reproducibility of the findings.

Thanks for the reviewer’s suggestion. Accordingly, for figure 1A, we have added the nuclear PKM2 ratio in astrocytes in control and different stages of EAE mice in Supplementary figure S1A. Moreover, the quantification of mean fluorescence intensity (MFI) for PKM2 was added in figure S1B. Moreover, we have added the number of animals used in each group in figure legend.

(2) The blue hue observed in the merged images of Figure 1B (lower panel) presents a challenge for interpretation. The source of this coloration remains unclear from the provided information. Did the authors also include a co-stain for the nucleus in their imaging? To enhance clarity, especially for individuals with color vision deficiency, the authors might consider utilizing different color combinations, such as presenting PKM2 in green and GFAP in magenta, which would aid in distinguishing the two components. Furthermore, for in vitro cell analysis, incorporating a nuclear stain could provide valuable insights into estimating the cytosolic-to-nuclear ratio of PKM2.

For the question relating to the merged images in figure 1B, PKM2 was presented in green, GFAP was presented in red and blue represents the nuclear staining by DAPI. “Merge” represents the merged images of these three colors. To enhance the clarity, we have added the images for the nuclear staining of DAPI.

(3) To substantiate the conclusion of the authors regarding the enhancement of aerobic glycolysis due to PKM2 expression and nuclear translocation in MOGsup-stimulated astrocytes, employing supplementary methodologies such as high-resolution respirometry and metabolomics could offer valuable insights. These techniques would provide a more comprehensive understanding of metabolic alterations and further validate the observed changes in glycolytic activity.

While we recognize the merits of techniques such as high-resolution respirometry and metabolomics, we believe that the conclusions regarding the enhancement of aerobic glycolysis due to PKM2 expression and nuclear translocation in MOGsup-stimulated astrocytes are sufficiently supported by the current experimental evidence. Our study has relied on a robust set of experiments, including lactate production, glucose consumption, cyto-nuclear localization analysis and western blotting analysis of key enzymes in glycolysis. These results, in conjunction with the literature on the role of PKM2 in various cancer cells, keratinocytes and immune cells, provide a strong foundation for our conclusions. Although metabolomics could offer a global view of the changes in metabolic states in astrocytes, as the end product of aerobic glycolysis is lactate, our study, which analyze the change of lactate levels in different experimental conditions might be more direct. However, we fully acknowledge that future studies employing these advanced methodologies could provide further insights into the precise mechanisms underlying PKM2's effects on aerobic glycolysis.

(4) Minor: Why is the style of the columns different in Gig 2 panel D compared to those shown in panels B, C, and G of Figure 2.

To maintain consistency in the column style across figure 2, we have updated the column in figure 2D. Now, we use same style of columns in Fig 2B, C, D and G.

(5) The effect of stimulating astrocytes with MOGsup on cell proliferation, as shown in Figure 2E, is very moderate. Does DASA-58 reduce the proliferation of control cells in this assay?

In response to the reviewer’s questions, we conducted a CCK8 analysis in astrocytes subjected to DASA-58 treatment. As depicted in Author response image 5, administration of DASA-58 did not reduce the proliferation of control cells. This result aligns with our other findings in the glycolysis assays and EdU analysis, where there is no statistical difference between control group and DASA-58-treated group. One plausible explanation for this is that in their steady state, astrocytes in the control group are not in a hyperproliferative state. Under such conditions, inhibiting the translocation of PKM2 via DASA-58 or other inhibitors did not significantly affect the proliferation of astrocytes.

Author response image 5.

CCK8 analysis of astrocyte proliferation. Primary astrocytes were pretreated with 50 μM DASA-58 for 30 min before stimulation with MOGsup. Data are represented as mean ± SEM. ***P<0.001. SEM, standard error of the mean.

(6) The tables and lists in Figure 4, panels A-D, are notably small, hindering readability and comprehension. Consider relocating these components to the supplementary materials as larger versions.

We have updated the tables and lists, the lines are made thicker. As suggested by the reviewer, we relocate theses components in Supplementary Figure S5.

Reviewer #3 (Recommendations For The Authors):

Higher magnification images that more clearly show nuclear translocation of PKM2 and pp65 and pSTAT3 immunoreactivity should be added to the figures panels, for example as inlets.

Thank you for pointing out this issue in the manuscript. According to the reviewer’s comments we have included higher magnification images as inlets for Figure 3A, Figure 3B and Figure 2A. These enlarged images now provide a clearer visualization of the nuclear translocation state of PKM2, pp65, and pSTAT3.

There are seldom wording errors like features => feathers at line 364.

We are very sorry for our incorrect writing. We have corrected this spelling mistake in the manuscript.

Reviewer #4 (Recommendations For The Authors):

Here below are major and minor concerns on the data presented:

(1) It is not clear from the Methods section what are the culture conditions defined as 'control' in Figure 1B-D. I believe the control should be culturing with the conditioned medium of normal (non-EAE) mice splenocytes to be sure the effect is not from cytokines naturally secreted by these cells.

Thanks for the reviewer’s comments and we totally understand the reviewer's concern. The control means non-treated primary astrocytes cultured with traditional DMEM medium supplemented with 10% FBS. In fact, we have performed experiments to exclude the possibility that the observed effect of MOGsup on the activation of astrocytes is from cytokines secreted by splenocytes. Splenocytes from normal (non-EAE) mice were isolated, cultured in RPMI-1640 medium containing 10% FBS for 60 hours, and supernatant was collected. Immunofluorescence staining of PKM2 and GFAP were performed in non-treated primary astrocytes and astrocytes stimulated with supernatant from control splenocytes. As shown in Figure S1C, in both groups, no difference was observed in PKM2 expression and localization, PKM2 was located mainly in the cytoplasm in theses conditions. These results indicate that observed effect of PKM2 in MOGsup-stimulated condition is not due to the cytokines secreted from splenocytes. Thus, we used non-treated primary astrocytes as controls in our study. To clarify the control group, we have revised the description in the figure legend, The revised expression is as follows: “Immunofluorescence staining of PKM2 (green) with GFAP (red) in non-treated primary astrocytes (control) or primary astrocytes cultured with splenocytes supernatants of MOG35–55-induced EAE mice (MOGsup) for different time points (6 h, 12 h and 24 h). ”

(2) Figure 3D: the presence of PMK2 in the nuclear fraction upon MOGSUP together with the DASA-58 (last lane of Figure 3D) is not supporting the hypothesis proposed and further may indicate that the reduction of pSTAT3, pp65, etc. observed is independent of PMK2 nuclear translocation/astrocyte activation being observed even in absence of MOGSUP.

Thank you for pointing out this problem in manuscript. The representing image of nuclear level of PKM2 in Figure 3D is not obvious, as shown by figure 3D, which has raised doubts among the reviewers. To strengthen our conclusion that the reduction of STAT3 and p65 pathway is related to the inhibited nuclear level of PKM2 induced by DASA-58, nuclear PKM2 level was quantified and added in Figure S4B. From the quantification results, it is evident that DASA-58 administration decreased the nuclear level of PKM2 in MOGsup-stimulated astrocytes. To address this concern, we have updated the immunoblot image for PKM2 in figure 3D and incorporated quantification results in supplementary Figure S4.

(3) Molecular docking indication and deletion co-immunoprecipitation reported in Figure 4 data are not concordant on TRIM21: N-terminal Phe23 and Thr87 (Figure 4E) predicted by MD to bind PMK2 are not in the PRY-SPRY domain suggested by the co-IP experiment (Figure 4I).

The discrepancy between the molecular docking prediction and the co-immunoprecipitation can be explained as follows:

Firstly, molecular docking is computational methods that predicts protein-protein interaction based on 3-D structures of the proteins. However, the accuracy of this predication can be influenced by the different models of 3D structures of TRIM21 and PKM2, as well as by factors such as post-translational modifications and flexibility of the proteins. Proteins in vivo are subject to post-translational modifications that can affect their interactions. These modifications are not fully captured in molecular docking analysis. For example, in our analysis, the predicted N-terminal Phe23 and Thr87 in TRIM21 hold the potential to interact with PKM2 by hydrogen bonds. However, such binding can be influenced by diverse biological environments, such as different cells and pathological conditions. Molecular docking predication may suggest the specific residues and binding pocked within the protein complex, however, the accuracy should be verified by experimental techniques such as immunoprecipitation. To address the predication results of molecular docking, the description has been revised as follows: “TRIM21 is predicted to bound to PKM2 via hydrogen bonds between the amino acids of the two molecules.”

Co-immunoprecipitation that involves the use of truncated domains of TRIM21 and PKM2, is an experimental technique relies on the specific interaction between antibody and targeted proteins. This technique can provide insights into the precise binding domains between TRIM21 and PKM2. As demonstrated in our study, PRY-SPRY domain of TRIM21 is involved in this binding. In summary, while molecular docking and Co-IP are valuable tools for studying protein-protein interactions, their differing focus and limitations may result in discrepancies between the predicted interaction sites and the experimentally identified interaction domains.

(4) The Authors state that PMK2 is a substrate of TRIM21 E3 ligase activity, however, this is not proved: i) interaction does not imply a ligase-substrate relationship; ii) the ubiquitination shown in Figure 6C is not performed in denaturing conditions thus the K63-Ub antibody can detect also interacting FLAG-IPed proteins (besides, only a single strong band is seen, not a chain; molecular weights in immunoblot should be indicated); iii) use of a catalytically inactive TRIM21 would be required as well.

We appreciate the reviewer’s comments regarding the limitations of the immunoprecipitation and K63-antibody test, which could not lead to the conclusion that PKM2 is a substrate of TRIM21. To avoid any misunderstandings, we have revised the relevant sentence from “Hereby, we recognized PKM2 as a substrate of TRIM21” to “Hereby, we recognized PKM2 as an interacting protein of TRIM21, and further studies are required to determine if it is a substrate of E3 ligase TRIM21”. Moreover, we have revised the title of the relevant part in the results section, the previous title, “TRIM21 ubiquitylates and promotes the nuclear translocation of PKM2” has been replaced with “TRIM21 promotes ubiquitylation and the nuclear translocation of PKM2”. Moreover, molecular weights for all proteins in western blotting were indicated.

(5) As above, molecular weights should always be indicated in immunoblot.

Thanks for pointing out this problem in the figures. Accordingly, we have added the molecular weights for every protein tested in immunoblot.

(6) The authors should describe the EAE mouse model in the text and in the material and methods as it may not be so well known to the entire reader audience, and the basic principle of MOG35-55 stimulation, in order to understand the experimental plan meaning.

We appreciate the reviewer’s comments highlighting the importance of clarifying EAE model for a broader understanding of the reader audience. In response, we have described the EAE model both in the text and in the materials and methods section. In the text, the description of EAE model was added at the beginning of the first paragraph in the Results section. The description is as follows: “EAE is widely used as a mouse model of multiple sclerosis, which is typically induced by active immunization with different myelin-derived antigens along with adjuvants such as pertussis toxin (PTX). One widely used antigen is the myelin oligodendrocyte glycoprotein (MOG) 35-55 peptide (Nitsch et al., 2021), which was adopted in our current studies.”

We have also added the detailed experimental procedures for EAE induction in the materials and methods section.

(7) The authors should better explain and give the rationale for the use of splenocytes and why directly activated astrocytes (isolated from the EAE model) cannot be employed to confirm/prove some of the presented data.

Firstly, splenocytes offer a heterogenous cell population, encompassing T cells and antigen presenting cells (APC), which may better mimic the microenvironment and complex immune responses observed in vivo.

Myelin oligodendrocyte glycoprotein (MOG) 35-55 peptide is one widely used antigen for EAE induction. MOG35-55 elicits strong T responses and is highly encephalitogenic. Moreover, MOG35-55 induces T cell-mediated phenotype of multiple sclerosis in animal models. Thus, by isolating splenocytes from the onset stage of EAE mice, which contains APC and effector T cells, followed by stimulation with antigen MOG35-55 in vitro for 60 hours, the T-cell response in the acute stage of EAE diseases could be mimicked in vitro. The supernatant from MOG35-55 stimulated splenocytes has high levels of IFN-γ and IL-17A, which in part mimic the pathological process and environment in EAE, and this technique has been documented in the references (Chen et al., 2009, Kozela et al., 2015).

Correspondingly, we have revised sentence for the use of MOG35-55 stimulates splenocytes in EAE mice and add the relevant references: “Supernatant of MOG35-55-stimulated splenocytes isolated from EAE mice were previously shown to elicit a T-cell response in the acute stage of EAE and are frequently used as an in vitro autoimmune model to investigate MS and EAE pathophysiology (Chen et al., 2009, Du et al., 2019, Kozela et al., 2015).”

Secondly, activated astrocytes (isolated from the EAE model) can not be employed for in vitro culture for the following reasons:

(1) Low cell viability. Compared to embryonic or neonatal mice, adult mice yield a limited number of viable cells. The is mainly because that adult tissues possess less proliferative capacity.

(2) Disease changes. Astrocytes in EAE mice are exposed to microenvironment including inflammatory cytokines, antigens and other pathological factors. Without this environment, the function and morphology of astrocytes undergo changes, which make it difficult to interpret the results in vitro.

For these reasons, the in vitro cultured primary astrocytes used the neonatal mice.

(8) The authors should indicate the phosphorylation sites they are referring to when analysing p-c-myc, pSTAT3, pp65, etc...

According to the reviewer’s suggestions, we have added the phosphorylation sites for pSTAT3 (Y705), pp65 (S536), p-c-myc (S62) and pIKK (S176+S180) in the figure panels.

(9) Reference of DASA-58 and TEPP-46 inhibitors and their specificity should be given.

According to the reviewer’s comments, we have added the relevant references for the use of DASA-58 and TEPP-46 as inhibitors of PKM2 nuclear transport. In primary BMDMs, LPS induced nuclear PKM2. However, driving PKM2 into tetramers using DASA-58 and TEPP-46 inhibited LPS-induced PKM2 nuclear translocation (Palsson-McDermott et al., 2015). Consistently, FSTL1 induced PKM2 nuclear translocation was inhibited by DASA-58 in BMDMs (Rao et al., 2022). Accordingly, we have added these references in the manuscript.

To address the selectivity of TEPP-46 and add the references, the relevant sentence has been revised from “TEPP-46 is an allosteric activator that blocks the nuclear translocation of PKM2 by promoting its tetramerization” to “TEPP-46 is a selective allosteric activator for PKM2, showing little or no effect on other pyruvate isoforms. It promotes the tetramerization of PKM2, thereby diminishing its nuclear translocation (Anastasiou et al., 2012, Angiari et al., 2020).”

Reviewing Editor (Recommendations For The Authors):

The reviewing editor would appreciate it if the original blots from the western blot analysis, which were used to generate the final figures, could be provided.

Thanks for the reviewing editor’s comment, accordingly, we will add the original blots for the western blots analysis.

References

Anastasiou D, Yu Y, Israelsen WJ, Jiang JK, Boxer MB, Hong BS, et al. Pyruvate kinase M2 activators promote tetramer formation and suppress tumorigenesis. Nature chemical biology 2012;8(10):839-47.

Escartin C, Guillemaud O, Carrillo-de Sauvage M-A. Questions and (some) answers on reactive astrocytes. Glia 2019;67(12):2221-47.

Ferrara G, Benzi A, Sturla L, Marubbi D, Frumento D, Spinelli S, et al. Sirt6 inhibition delays the onset of experimental autoimmune encephalomyelitis by reducing dendritic cell migration. Journal of neuroinflammation 2020;17(1):228.

Lin CC, Edelson BT. New Insights into the Role of IL-1β in Experimental Autoimmune Encephalomyelitis and Multiple Sclerosis. Journal of immunology (Baltimore, Md : 1950) 2017;198(12):4553-60.

Palsson-McDermott Eva M, Curtis Anne M, Goel G, Lauterbach Mario AR, Sheedy Frederick J, Gleeson Laura E, et al. Pyruvate Kinase M2 Regulates Hif-1α Activity and IL-1β Induction and Is a Critical Determinant of the Warburg Effect in LPS-Activated Macrophages. Cell metabolism 2015;21(1):65-80.Rao J, Wang H, Ni M, Wang Z, Wang Z, Wei S, et al. FSTL1 promotes liver fibrosis by reprogramming macrophage function through modulating the intracellular function of PKM2. Gut 2022;71(12):2539-50.

Wheeler MA, Clark IC, Tjon EC, Li Z, Zandee SEJ, Couturier CP, et al. MAFG-driven astrocytes promote CNS inflammation. Nature 2020;578(7796):593-9.

Zhang J, Feng G, Bao G, Xu G, Sun Y, Li W, et al. Nuclear translocation of PKM2 modulates astrocyte proliferation via p27 and -catenin pathway after spinal cord injury. Cell Cycle 2015;14(16):2609-18.

Author response:

We thank the editor and reviewers for their supportive comments about our modeling approach and conclusions, and for raising several valid concerns; we address them briefly below.

Concerns about model’s biological realism and impact on interpretations

The goal of this paper was to use an interpretable and modular model to investigate the impact of varying sensorimotor delays. Aspects of the model (e.g. layered architecture, modularity) are inspired by biology; at the same time, necessary abstractions and simplifications (e.g. using an optimal controller) are made for interpretability and generalizability, and they reflect common approaches from past work. The hypothesized effects of certain simplifying assumptions are discussed in detail in Section 3.5. Furthermore, the modularity of our model allows us to readily incorporate additional biological realism (e.g. biomechanics, connectomics, and neural dynamics) in future work. In the revision, we will add citations and edits to the text to clarify these points.

Concerns that the model is overly complex

To investigate the impact of sensorimotor delays on locomotion, we built a closed-loop model that recapitulates the complex joint trajectories of fly walking. We agree that locomotion models face a tradeoff between simplicity/interpretability and realism — therefore, we developed a model that was as simple and interpretable as possible, while still reasonably recapitulating joint trajectories and generalizing to novel simulation scenarios. Along these lines, we also did not select a model that primarily recreates empirical data, as this would hinder generalizability and add unnecessary complexity to the model. We do not think these design choices are significant weaknesses of this model; in fact, few comparable models account for all joints involved in locomotion, and fewer explicitly compare model kinematics with kinematics from data. We will add citations and edits to the text to clarify these points in the revision.

Concerns about the validity of the Kinematic Similarity (KS) metric to evaluate walking

We chose to incorporate only the first two PCA modes dimensions in the KS metric because the kernel density estimator performs poorly for high dimensional data. Our primary use of this metric was to indicate whether the simulated fly continues walking in the presence of perturbations. For technical reasons, it is not feasible to perform equivalent experiments on real walking flies, which is one of the reasons we explore this phenomenon with the model. We note the dramatic shift from walking to non-walking as delay increases (Figure 5). To be thorough, in the revision, we will investigate the effect of incorporating additional PCA modes, and whether this affects the interpretation of our results. We will additionally edit the discussion and presentation of the KS metric to clarify its purpose in this study. We agree with the reviewers that the KS metric is too coarse to reflect fine details of joint kinematics; indeed, in the unperturbed case, we evaluate our model’s performance using other metrics based on comparisons with empirical data (Figures 2, 7, 8).

Author response:

We thank the reviewers for their engagement and constructive comments. This provisional response aims to clarify key misconceptions, address major criticisms, and outline our revision plans.

A primary concern of the reviewers appears to be our model's limitations in addressing a broad range of empirical findings. This, however, misinterprets our core contribution. Our work centers on a cautionary tale that before advocating for newly discovered cell types and their purported special roles in spatial cognition—an approach prevalent in the field—such claims must be tested against alternative (null) hypotheses that may contradict intuitive expectations. We present such an alternative hypothesis regarding spatial cells and their assumed privileged roles. We show that key findings in the field - spatial “cell types”,  arise in a set of null models without spatial grounding (including untrained variants) despite the models not being a model for spatial processing, and we also found that they had no privileged role for representing spatial information.

Our proposal is not a new model attempting to explain the brain, and therefore we do not aim to capture every empirical finding. Indeed, we would not expect an object recognition model (and its untrained variant) with no explicit spatial grounding to account for all phenomena in spatial cognition. This underscores our key point: if there exists a basic, spatially agnostic model that can explain certain degrees of empirical findings using criteria from the literature (i.e. place, head-direction and border cells), what implications does this have for the more complex theories and models proposed as underlying mechanisms of special cell types?

Regarding concerns about the limited scope and generalizability of our setting, we will clarify that we considered multiple DNN architectures, both trained and untrained, on multiple decoding tasks (position, head direction, and nearest-wall distance). We plan to extend our experiments further as detailed in the revision plan below.

Further, there was a methodological concern about using a linear decoder on a fixed DNN for spatial decoding tasks being a form of "hacking". However, linear readout is standard practice in neuroscience to characterize information available in a neural population. Moreover, our tests on untrained networks also showed spatial decoding capabilities, suggesting it's not solely due to the linear readout.

For our full revision plan:

(1) We will revise the manuscript to better reflect these above points, clarifying our paper's stance and improving the writing to reduce misconceptions.

(2) We will address individual public reviews in more detail.

(3) We intend to address key reviewer recommendations, focusing on better situating our work within the broader context of the existing literature whilst emphasizing the null hypothesis perspective.

(4) In general, we will consider additional aspects of the literature and conduct new experiments to strengthen the relevance of our work to existing work. We highlight a number of potential experiments which we believe can address reviewer concerns:

a. Blurring the visual inputs to DNNs to match rodent perception.

b. Vary environmental settings to verify whether our findings are more

generalizable (which we predict to be the case).

c. Vary the environment to assess remapping effects, which will strengthen the

connection of our work to the literature.

Author response:

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

Public Reviews

Reviewer #1 (Public Review):

Summary:

Federer et al. tested AAVs designed to target GABAergic cells and parvalbumin-expressing cells in marmoset V1. Several new results were obtained. First, AAV-h56D targeted GABAergic cells with >90% specificity, and this varied with serotype and layer. Second, AAV-PHP.eB.S5E2 targeted parvalbumin-expressing neurons with up to 98% specificity. Third, the immunohistochemical detection of GABA and PV was attenuated near viral injection sites.

Strengths:

Vormstein-Schneider et al. (2020) tested their AAV-S5E2 vector in marmosets by intravenous injection. The data presented in this manuscript are valuable in part because they show the transduction pattern produced by intraparenchymal injections, which are more conventional and efficient.

Our manuscript additionally provides detailed information on the laminar specificity and coverage of these viral vectors, which was not investigated in the original studies.

Weaknesses:

The conclusions regarding the effects of serotype are based on data from single injection tracks in a single animal. I understand that ethical and financial constraints preclude high throughput testing, but these limitations do not change what can be inferred from the measurements. The text asserts that "...serotype 9 is a better choice when high specificity and coverage across all layers are required". The data presented are consistent with this idea but do not make a strong case for it.

We are aware of the limitations of our results on the AAV-h56D. We agree with the Reviewer that a single injection per serotype does not allow us to make strong statements about differences between the 3 serotypes. Therefore, in the revised version of the manuscript we have tempered our claims about such differences and use more caution in the interpretation of these data (Results p. 6 and Discussion p.10). Despite this weakness, we feel that these data still demonstrate high efficiency and specificity across cortical layers of transgene expression in GABA cells using the h56D promoter, at least with two of the 3 AAV serotypes we tested. We feel that in itself this is sufficiently useful information for the primate community, worthy of being reported. Due to cost, time and ethical considerations related to the use of primates, we chose not to perform additional experiments to determine precise differences among serotypes. Thus, for example, while it is possible that had we replicated these experiments, serotype 7 could have proven equally efficient and specific as the other two serotypes, we felt answering this question did not warrant additional experiments in this precious species.

A related criticism extends to the analysis of Injection volume on viral specificity. Some replication was performed here, but reliability across injections was not reported. My understanding is that individual ROIs were treated as independent observations. These are not biological replicates (arguably, neither are multiple injection tracks in a single animal, but they are certainly closer). Idiosyncrasies between animals or injections (e.g., if one injection happened to hit one layer more than another) could have substantial impacts on the measurements. It remains unclear which results regarding injection volume or serotype would hold up had a large number of injections been made into a large number of marmosets.

For the AAV-S5E2, we made a total of 7 injections (at least 2 at each volume), all of which, irrespective of volume, resulted in high specificity and efficiency for PV interneurons. Our conclusion is that larger volumes are slightly less specific, but the differences are minimal and do not warrant additional injections. Additionally, we kept all the other parameters across animals constant (see new Supplementary Table 1), all of our injections involved all cortical layers, and the ROIs we selected for counts encompassed reporter protein expression across all layers. To provide a better sense of the reliability of the results across injections, in the revised version of the manuscript we now provide results for each of the AAV-S5E2 injection case separately in a new Supplementary Table 2. The results in this table indicate the results are indeed rather consistent across cases with slightly greater specificity for injection volumes in the range of 105-180 nl.

Reviewer #2 (Public Review):

This is a straightforward manuscript assessing the specificity and efficiency of transgene expression in marmoset primary visual cortex (V1), for 4 different AAV vectors known to target transgene expression to either inhibitory cortical neurons (3 serotypes of AAV-h56D-tdTomato) or parvalbumin (PV)+ inhibitory cortical neurons in mice. Vectors are injected into the marmoset cortex and then postmortem tissue is analyzed following antibody labeling against GABA and PV. It is reported that: "in marmoset V1 AAV-h56D induces transgene expression in GABAergic cells with up to 91-94% specificity and 80% efficiency, depending on viral serotype and cortical layer. AAV-PHP.eB-S5E2 induces transgene expression in PV cells across all cortical layers with up to 98% specificity and 86-90% efficiency."

These claims are largely supported but slightly exaggerated relative to the actual values in the results presented. In particular, the overall efficiency for the best h56D vectors described in the results is: "Overall, across all layers, AAV9 and AAV1 showed significantly higher coverage (66.1{plus minus}3.9 and 64.9%{plus minus}3.7)". The highest coverage observed is just in middle layers and is also less than 80%: "(AAV9: 78.5%{plus minus}9.1; AAV1: 76.9%{plus minus}7.4)".

In the abstract, we indeed summarize the overall data and round up the decimals, and state that these percentages are upper bound but that they vary by serotype and layer while in the Results we report the detailed counts with decimals. To clarify this, in the revised version of the Abstract we have changed 80% to 79% and emphasize even more clearly the dependence on serotype and layer. We have amended this sentence of the Abstract as follows: “We show that in marmoset V1 AAV-h56D induces transgene expression in GABAergic cells with up to 91-94% specificity and 79% efficiency, but this depends on viral serotype and cortical layer.”

For the AAV-PHP.eB-S5E2 the efficiency reported in the abstract (“86-90%) is also slightly exaggerated relative to the results: “Overall, across all layers coverage ranged from 78%{plus minus}1.9 for injection volumes >300nl to 81.6%{plus minus}1.8 for injection volumes of 100nl.”

Indeed, the numbers in the Abstract are upper bounds, for example efficiency in L4A/B with S5E2 reaches 90%. To further clarify this important point, in the revised abstract we now state ”AAV-PHP.eB-S5E2 induces transgene expression in PV cells across all cortical layers with up to 98% specificity and 86-90% efficiency, depending on layer”.

These data will be useful to others who might be interested in targeting transgene expression in these cell types in monkeys. Suggestions for improvement are to include more details about the vectors injected and to delete some comments about results that are not documented based on vectors that are not described (see below).

Major comments:

Details provided about the AAV vectors used with the h56D enhancer are not sufficient to allow assessment of their potential utility relative to the results presented. All that is provided is: "The fourth animal received 3 injections, each of a different AAV serotype (1, 7, and 9) of the AAV-h56D-tdTomato (Mehta et al., 2019), obtained from the Zemelman laboratory (UT Austin)." At a minimum, it is necessary to provide the titers of each of the vectors. It would also be helpful to provide more information about viral preparation for both these vectors and the AAVPHP.eB-S5E2.tdTomato. Notably, what purification methods were used, and what specific methods were used to measure the titers?

We thank the Reviewer for this comment. In the revised version of the manuscript, we now provide a new Supplementary Table 1 with titers and other information for each viral vector injection. We also provide information regarding viral preparation in a new sections in the Methods entitled “ Viral Preparation”  (p12).

The first paragraph of the results includes brief anecdotal claims without any data to support them and without any details about the relevant vectors that would allow any data that might have been collected to be critically assessed. These statements should be deleted. Specifically, delete: “as well as 3 different kinds of PV-specific AAVs, specifically a mixture of AAV1-PaqR4-Flp and AAV1-h56D-mCherry-FRT (Mehta et al., 2019), an AAV1-PV1-ChR2-eYFP (donated by G. Horwitz, University of Washington),” and delete “Here we report results only from those vectors that were deemed to be most promising for use in primate cortex, based on infectivity and specificity. These were the 3 serotypes of the GABA-specific pAAV-h56D-tdTomato, and the PV-specific AAVPHP.eB-S5E2.tdTomato.” These tools might in fact be just as useful or even better than what is actually tested and reported here, but maybe the viral titer was too low to expect any expression.

These data are indeed anecdotal, but we felt this could be useful information, potentially preventing other primate labs from wasting resources, animals and time, particularly, as some of these vectors have been reported to be selective and efficient in primate cortex, which we have not been able to confirm. We made several injections in several animals of those vectors that failed either to infect a sufficient number of cells or turned out to be poorly specific. Therefore, the negative results have been consistent in our hands. But we agree with the Reviewer that our negative results could have depended on factors such as titer. In the revised version of the manuscript, following the reviewer’s suggestion, we have deleted this information.

Based on the description in the Methods it seems that no antibody labeling against TdTomato was used to amplify the detection of the transgenes expressed from the AAV vectors. It should be verified that this is the case - a statement could be added to the Methods.

That is indeed the case. We used no immunohistochemistry to enhance the reporter proteins as this was unnecessary. The native/ non-amplified tdT signal was strong. This is now stated in the methods (p.12).

Reviewer #3 (Public Review):

Summary:

Federer et al. describe the laminar profiles of GABA+ and of PV+ neurons in marmoset V1. They also report on the selectivity and efficiency of expression of a PV-selective enhancer (S5E2). Three further viruses were tested, with a view to characterizing the expression profiles of a GABA-selective enhancer (h56d), but these results are preliminary.

Strengths:

The derivation of cell-type specific enhancers is key for translating the types of circuit analyses that can be performed in mice - which rely on germline modifications for access to cell-type specific manipulation - in higher-order mammals. Federer et al. further validate the utility of S5E2 as a PV-selective enhancer in NHPs.

Additionally, the authors characterize the laminar distribution pattern of GABA+ and PV+ cells in V1. This survey may prove valuable to researchers seeking to understand and manipulate the microcircuitry mediating the excitation-inhibition balance in this region of the marmoset brain.

Weaknesses:

Enhancer/promoter specificity and efficiency cannot be directly compared, because they were packaged in different serotypes of AAV.

The three different serotypes of AAV expressing reporter under the h56D promoter were only tested once each, and all in the same animal. There are many variables that can contribute to the success (or failure) of a viral injection, so observations with an n=1 cannot be considered reliable.

This is an important point that was also brough up by Reviewer 1, which we have addressed in our reply-to-Reviewer 1. For clarity and convenience, below we copy our response to Reviewer 1.

“We are aware of the limitations of our results on the AAV-h56D. We agree with the Reviewer that a single injection per serotype does not allow us to make strong statements about differences between the 3 serotypes. Therefore, in the revised version of the manuscript we will temper our claims about such differences and use more caution in the interpretation of these data. Despite this weakness, we feel that these data still demonstrate high efficiency and specificity across cortical layers of transgene expression in GABA cells using the h56D promoter, at least with two of the 3 AAV serotypes we tested. We feel that in itself this is sufficiently useful information for the primate community, worthy of being reported. Due to cost, time and ethical considerations related to the use of primates, we chose not to perform additional experiments to determine precise differences among serotypes. Thus, for example, while it is possible that had we replicated these experiments, serotype 7 would have proven equally efficient and specific as the other two serotypes, we felt answering this question did not warrant additional experiments in this precious species.”

The language used throughout conflates the cell-type specificity conferred by the regulatory elements with that conferred by the serotype of the virus.

Authors’ reply. In the revised version of the manuscript, we have corrected ambiguous language throughout.

Recommendations for the authors

Reviewer #1 (Recommendations For The Authors):

My Public Review comments can be addressed by dialing down the interpretation of the data or providing appropriate caveats in the presentation of the relevant results and their discussion.

We have done so. See text additions on p. 6 of the Results and p.10 of the Discussion.

Minor comments:

92% of PV+ neurons in the marmoset cortex were GABAergic. Can the authors speculate on the identity of the 8% PV+/GABA- neurons (e.g., on the basis of morphology)? Are they likely excitatory? Are they more likely to represent failures of GABA staining?

We do not know what the other 8% of PV+/GABA- neurons are because we did not perform any other kind of IHC staining. Our best guess is that at least to some extent these represent failures of GABA staining, which is always challenging to perform in primate cortex. However, in mouse PV expression has been demonstrated in a minority of excitatory neurons.

"Coverage of the PV-AAV was high, did not depend on injection volume.." The fact that the coverage did not depend on injection volume presumably depends, at least in part, on how ROIs were selected. Surely different volumes of injection transduce different numbers of neurons at different distances from the injection track. This should be clarified.

The ROIs were selected at the center of the injected site/expression core from sections in which the expression region encompassed all cortical layers. Of course, larger volumes of injection resulted in larger transduced regions and therefore overall larger number of transduced neurons, but we counted cells only withing 100 µm wide ROIs at the center of the injection and the percent of transduced PV cells in this core region did not vary significantly across volumes. We have clarified the methods of ROI selection (see Methods pp. 13).

Figure 2. What is meant by “absolute” in the legend for Figure 2? (How does “mean absolute density” differ from “mean density?”)

We meant not relative, but this is obvious from the units, so we have removed the word “absolute” in the legend.

Some non-significant p-values are indicated by "p>0.05" whereas others are given precisely (e.g., p = 1). Please provide precise p-values throughout. Also, the p-value from a surprisingly large number of comparisons in the first section of the results is "1". Is this due to rounding? Is it possible to get significance in a Bonferroni-corrected Kruskal-Wallis test with only 6 observations per condition?

We now report exact p values throughout the manuscript (with a couple of exceptions where, in order to avoid reporting a large number of p values which interrupts the flow of the manuscript) we provide the upper bound value and state all those comparisons were below that value). The minimum sample size for Kruskall Wallis is 5, for each group being compared, and we our sample is 6 per group.

Figure 3: The density of tdTomato-expressing cells appears to be greater at the AAV9 injection site than at the AAV1 injection site in the example sections shown. Might some of the differences between serotypes be due to this difference? I would imagine that resolving individual cells with certainty becomes more difficult as the amount of tdTomato expression increases.

There was an error in the scale bar of Fig. 3C, so that the AAV1 injection site was shown at higher magnification than indicated by the wrong scale bar. Hence the density of tdTomato appeared lower than it is. Moreover, the tdT expression region shown in Fig. 3A is a merge of two sections, while it is only from a single section in panels B and C, leading to the impression of higher density of infected cells in panel A. The pipette used for the injection in panel A was not inserted perfectly vertical to the cortical surface, resulting in an injection site that did not span all layers in a single section; thus, to demonstrate that the injection indeed encompassed all layers (and that the virus infected cells in all layers), we collapsed label from two sections. We have now corrected the magnification of panel C so that it matches the scale bar in panel A, and specify in the figure legend that panel A label is from two sections.

Text regarding Figure 3: The term “injection sizes” is confusing. I think it is intended to mean “the area over which tdTomato-expressing cells were found” but this should be clarified.

Throughout the manuscript, we have changed the term injection site to “viral-expression region”.

Figure 3: What were the titers of the three AAV-h56D vectors?

Titers are now reported in the new Supplementary Table 1.

Figure 3: The yellow box in Figure 3C is slightly larger than the yellow boxes in 3A and 3B. Is this an error or should the inset of Figure 3 have a scale bar that differs from the 50 µm scale bar in 3A?

There were indeed errors in scale bars in this figure, which we have now corrected. Now all boxes have the same scale bar.

Was MM423 one of the animals that received the AAV-h56D injections or one of the three that received AAV-S5E2 injection?

This is an animal that received a 315nl injection of AAV-PHP.eB-S5E2.tdTomato. This is now specified in the Methods (see p. 12) and in the new Supplementary Table 1.

Please provide raw cell counts and post-injection survival times for each animal.

We now provide this information in Supplementary Tables 1 and 2.

How were the different injection volumes of the AAV-S5E2 virus arranged by animal? Which volume of the AAV-S5E2 virus was injected into the two animals who received single injections?

We now provide this information in Supplementary Table 1.

Figure 6A: the point is made in the text that "[the distribution of tdT+ and PV+ neurons] did not differ significantly... peaking in L2/3 and 4C " Is the fact that the number of tdT+ and PV+ peak in layers 2/3 and 4C a consequence of these layers being thicker than the others? If so, this statement seems trivial.

No, and this is the reason why we measured density in addition to percent of cells across layers in Figure 2. Figure 2B shows that even when measuring density, therefore normalizing by area, GABA+ and PV+ cell density still peaks in L2/3 and 4. Thus, these peaks do not simply reflect the greater thickness of these layers.

Do the authors have permission to use data from Xu et al. 2010?

Yes, we do.

Reviewer #2 (Recommendations For The Authors):

Minor comments:

"Viral strategies to restrict gene expression to PV neurons have also been recently developed (Mehta et al., 2019; Vormstein-Schneider et al., 2020)." Mich et al. should also be cited here. Cell Rep. 2021;34(13):108754.

We thank the reviewer for pointing out this missing references. This is now cited.

“GABA density in L4C did not differ from any other layers, but the percent of GABA+ cells in L4C was significantly higher than in L1 (p=0.009) and 4A/B (p=<0.0001).” This and other similar observations depend on calculating the percentage of cells relative to the total number of DAPI-labeled cells in each layer. Since it is apparent that there must be considerable variability between layers, it would be helpful to add a histogram showing the densities of all DAPI-labeled cells for each layer.

This is not how we calculated density. Density, as now clarified in the Results on p. 4, was defined as the number of cells per unit area. Counts in each layer were divided by each layers’ counting area. This corrects for differences in number of total labeled cells per layer. Therefore, reporting DAPI density is not necessary (we did not count DAPI cell density per layer).

"Identical injection volumes of each serotype, delivered at 3 different cortical depths (see Methods), resulted in different injection sizes, suggesting the different serotypes have different capacity of infecting cortical neurons. AAV7 produced the smallest injection site, which additionally was biased to the superficial and deep layers, with only few cells expressing tdT in the middle layers (Fig. 3B). AAV9 (Fig. 3A) and AAV1 (Fig. 3C) resulted in larger injection sites and infected all cortical layers." Differences noted here might reflect either differences related to the AAV serotype or to differences in titers. Please add details about titers for each vector and add comments as appropriate. Another interpretation would be that there are differences in viral spread within the tissue.

We have now added Supplementary Table 1 which reports titers in addition to other information about injections. The titers and volumes used for AAV9 and AAV7 were identical, while the titer for AAV1 was higher. Therefore, the differences in infectivity, particularly the much smaller expression region obtained with AAV7 cannot be attributed to titer. Likely this is due to differences in tropism and/or viral spread among serotypes. This is now discussed (see Results p. 5bottom and 6 top).

“Recently, several viral vectors have been identified that selectively and efficiently restrict gene expression to GABAergic neurons and their subtypes across several species, but a thorough validation and characterization of these vectors in primate cortex has lacked.” Is this really a fair statement, or is the characterization presented here also lacking? Methods used by others for quantifying specificity and efficiency are essentially the same as used here. See for example Mich et al. (which is not cited).

The original validation in primates of the vectors examined in our study was based on small tissue samples and did not examine the laminar expression profile of transgene expression induced by these enhancer-AAVs. For example, the validation of the h56D-AAV in marmoset cortex in the original paper by Mehta et al (2019) was performed on a tissue biopsy with no knowledge of which cortical layers were included in the tissue sample. The only study that shows laminar expression in primate cortex (Mich et al., which is now cited), only shows qualitative images of viral expression across layers, reporting total specificity and coverage pooled across samples; moreover, the study by Mich et al.  deals with different PV-specific enhancers than the ones characterized in our study. Unlike any of the previous studies, here we have quantified specificity and coverage across layers.

"Specifically, we have shown that the GABA-specific AAV9-h56D (Mehta et al., 2019) induces transgene expression in GABAergic cells with up to 91-94% specificity and 80% coverage, and the PV-specific AAV-PHP.eB-S5E2 (Vormstein-Schneider et al., 2020) induces transgene expression in PV cells with up to 98% specificity and 86-90% coverage." These statements in the discussion repeat the somewhat exaggerated coverage numbers noted above for the Abstract.

The averages across all layers are reported in the Results. The Discussion, abstract and discussion report upper limits, and this is made clear by stating “up to”, and now we have also added “depending on layer”.

Reviewer #3 (Recommendations For The Authors):

Abstract:

• Ln 2: Can you be more specific about what you mean by the 'various functions of inhibition'? e.g. do you mean 'the various inhibitory influences on the local microcircuit' or similar?

These are listed in the introduction to the paper but there is no space in the abstract to do so. Now the sentence reads: “various computational functions of…”.

• Ln 5: 'has' to 'is'/'has been'.

The grammar here is correct “has derived”.

• Ln 6: humans are primates! Maybe change this to 'nonhuman primates'?

We have added “non-human”

• Ln n-1: 'viral vectors represent' -> 'viral vectors are'.

We have changed it to “are”

Intro:

• Many readers may expect 'VIP' to be listed as the third major sub-class of interneurons. Could you note that the 5HT3a receptor-expressing group includes VIP cells?

Done (p.3).

• "Understanding cortical inhibitory neuron function in the primate is critical for understanding cortical function and dysfunction in the model system closest to humans" - this seems close to being circular logic (not quite, but close). Could you modify this sentence to reflect why understanding cortical function and dysfunction in NHP may be of interest?

This sentence now reads (p.3):” Understanding cortical inhibitory neuron function in the primate is critical for understanding cortical function and dysfunction in the model system closest to humans, where cortical inhibitory neuron dysfunction has been implicated in many neurological and psychiatric disorders, such as epilepsy, schizophrenia and Alzheimer’s disease (Cheah et al., 2012; Verret et al., 2012; Mukherjee et al., 2019)”. We also note that this was already stated in the previous version of the paper but in the Discussion section which read (and still reads on p. 9 2nd paragraph): “It is important to study inhibitory neuron function in the primate, because it is unclear whether findings in mice apply to higher species, and inhibitory neuron dysfunction in humans has been implicated in several neurological and psychiatric disorders (Marin, 2012; Goldberg and Coulter, 2013; Lewis, 2014).”.

• "In particular, two recent studies have developed recombinant adeno-associated viral vectors (AAV) that restrict gene expression to GABAergic neurons". This sentence places the emphasis on the wrong component of the technology. The fact that AAV was used is irrelevant; these constructs could equally have been packaged in a lenti, CAV, HSV, rabies, etc. The emphasis should be on the recently developed regulatory elements (the enhancers/promoters).

Same problem with the following excerpts; this text implies that the serotype/vector confers cell-type selectivity, but the results presented do not support this assertion (the promoter/enhancer is what confers the selectivity).

• "specifically, three serotypes of an AAV that restricts gene expression to GABAergic neurons".

• "one serotype of an AAV that restricts gene expression to PV cells".

• "GABA- and PV-specific AAVs".

• "GABA-specific AAV" (in results).

• "PV-specific AAVs".

• "In this study, we have characterized several AAV vectors designed to restrict expression to GABAergic cells" (in discussion).

• "GABA-virus". GABA is a NT, not a virus.

We have modified the language in all these sections and throughout the manuscript.

Results:

• Enhancer specificity and efficiency cannot be directly compared, because they were packaged in different serotypes of AAV.

We agree, and in fact we are not making comparisons between different enhancers (i.e., S5E2 and h56D).

The three different serotypes of AAV expressing reporter under the h56D promoter were only tested once each, and all in the same animal. There are many variables that can contribute to the success (or failure) of a viral injection, so observations with an n=1 cannot be considered reliable.

The authors need to either: (1) replicate the h56D virus injections in (at least) a second animal, or (2) rewrite the paper to focus on the AAV.PhP mDlx virus alone - for which they have adequate data - and mention the h56D data as an anecdotal result, with clear warnings about the preliminary nature of the observations due to lack of replication.

We agree about the lack of sufficient data to make strong statements about the differences between serotypes for the h56D-AAV. In the revised version of the manuscript, following the Reviewers’ suggestion, we have chosen to temper our claims about differences between serotypes for the h56D enhancer and use more caution in the interpretation of these data. We feel that these data still demonstrate sufficiently high efficiency and specificity across cortical layers of transgene expression in GABA cells using the h56D promoter, at least with two of the 3 AAV serotypes we tested, to warrant their use in primates. Due to cost, time and ethical considerations related to the use of primates, we chose not to perform additional experiments to determine precise differences among serotypes. Thus, for example, while it is possible that had we replicated these experiments, serotype 7 could have proven equally efficient and specific as the other two serotypes, we felt answering this question did not warrant additional experiments in this precious species. Our edits in regard to this point can be found in the Results on p. 6 and Discussion on p. 10.

• Did the authors compare h56D vs mDlx? This would be a useful and interesting comparison.

We did not.

• 3 tissue sections were used for analysis. How were these selected? Did the authors use a stereological approach?

For the analysis in Fig. 2, the 3 sections were randomly selected and for the positioning of the ROIs we selected a region in dorsal V1 anterior to the posterior pole  (to avoid laminar distortions due to the curvature of the brain). This is now specified (see p. 4).

• "both GABA+ and PV+ cells peak in layers" revise for clarity (e.g., the counts peak).

In now reads “GABA+ and PV+ cell percent and density” (see p.4).

• "we refer to this virus as GABA-AAV" these are 3 different viruses!

The idea here was to use an abbreviation instead of using the full viral name every single time. Clearly the reviewer does not like this, so we have removed this convention throughout the paper and now specify the entire viral name each time.

• "Identical injection volumes of each serotype, delivered at 3 different cortical depths (see Methods), resulted in different injection sizes". Do you mean 'resulted in different volumes of expression'?

Yes. We have now rephrased this as follows: “…resulted in viral expression regions that differed in both size as well as laminar distribution” (p.5).

• “suggesting the different serotypes have different capacity of infecting cortical neurons”. You can’t draw any firm conclusions from a single injection. The rest of this section of the results, along with the whole of Figure 4, and Figure 7a-d, is in danger of being misleading. Please remove. The best you can do here is to say ‘we injected 3 different viruses that express reporter under the h56D promoter. The results are shown in Figure 3, but these are anecdotal, as only a single injection of each virus was performed’. You could then note in the discussion to what extent these results are consistent with the existing literature (e.g., AAV9 often produces good coverage in NHP – anterograde and retrograde, AAV1 also works well in the CNS, although generally doesn’t infect as aggressively as AAV9. I’m not familiar with any attempts to use AAV7).

With respect to Fig. 4, our approach in the revised version is detailed above. For convenience we copy it below here. With respect to Fig 7A-D, we feel the results are more robust as the data from the 3 serotypes here were pooled together, as the 3 serotype similarly downregulated GABA and PV expression at the injection site, and we do not make any statement about differences among serotypes for the data shown in Fig. 7A-D.

“In the revised version of the manuscript, following the Reviewer ’s suggestion, we have chosen to temper our claims about differences between serotypes for the h56D enhancer and use more caution in the interpretation of these data (see revised text in the Results on p. 6 and in the Discussion on p. 10). We feel that these data still demonstrate sufficiently high efficiency and specificity across cortical layers of transgene expression in GABA cells using the h56D promoter, at least with two of the 3 AAV serotypes we tested, to warrant their use in primates. Due to cost, time and ethical considerations related to the use of primates, we chose not to perform additional experiments to determine precise differences among serotypes. Thus, for example, while it is possible that had we replicated these experiments, serotype 7 could have proven equally efficient and specific as the other two serotypes, we felt answering this question did not warrant additional experiments in this precious species.”

• Figure 3: why the large variation in tissue quality? Are the 3 upper images taken at the same magnification? If not, they need different scale bars. The cells in A (upper row) look much smaller than those in B and C, and the size of the 'inset' box varies.

We thank the reviewer for noticing this. We discovered an error in the scale bar of Fig. 3C, so that the AAV1 injection site was shown at higher magnification than indicated by the wrong scale bar. We have now corrected the error in scale bars. We have also fixed the different box sizes.

• "Overall, across all layers coverage ranged from 78%{plus minus}1.9 for injection volumes >300nl to 81.6%{plus minus}1.8 for injection volumes of 100nl." Coverage didn't differ between layers, so revise this to: "Overall, across all layers coverage ranged from 78% to 81.6%." or give an overall mean (~80%).

We have corrected the sentence as suggested by the Reviewer (see p. 8 first paragraph).

• "extending farther from the borders" -> "extending beyond the borders".

We have corrected the sentence as suggested by the Reviewer (see p. 8).

• "The reduced GABA and PV immunoreactivity caused by the viruses implies that the specificity of the viruses we have validated in this study is likely higher than estimated". Yes, but for balance you should also note that they may harm the physiology of the cell.

We have added a sentence acknowledging this to the Discussion. Specifically, on p. 10, we now state: “However, this reduced immunoreactivity raises concerns about the virus or high levels of reporter protein possibly harming the cell physiology.”

Discussion:

• "but a thorough validation and characterization of these vectors in primate cortex has lacked" better to say "has been limited", because Dimidschstein 2016 (marmoset V1) and Vormstein-schneider 2020 (macaque S1 and PFC) both reported expression in NHP.

We have added the following sentence to this paragraph of the Discussion. “In particular, previous studies have not characterized the specificity and coverage of these vectors across cortical layers.”(see p. 8).

• "whether finding in mice" -> 'whether findings in mice'.

Corrected, thanks.

• The discussion re: species differences is missing reference to Kreinen 2020 (10.1038/s41586-020-2781-z).

This reference has been added. Thanks.

• “Injections of about 200nl volume resulted in higher specificity (95% across layers) and coverage” – this is misleading. The coverage was not statistically different among injection volumes.

We have added the following sentence: ”although coverage did not differ significantly across volumes.” (see p. 10).

• "it is possible that subtle alteration of the cortical circuit upon parenchymal injection of viruses (including AAVs) leads to alteration of activity-dependent expression of PV and GABA." Or (and I would argue, more likely) the expression of large quantities of your big reporter protein compromised the function of the cell, leading to reduced expression of native proteins. You don't mention any IHC to amplify the RFP signal, so I'm assuming that your images are of direct expression. If so, you are expressing A LOT of reporter protein.

We have added a sentence acknowledging this to the Discussion. Specifically, on p. 10, we now state: “However, this reduced immunoreactivity raises concerns about the virus or high levels of reporter protein possibly harming the cell physiology.”

Methods:

• It's difficult to piece together which viruses were injected in which monkeys, at what volumes, and at what titer. Please compile this info into a table for ease of reference (including any other relevant parameters).

We now provide a Supplementary Table 1.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors of this manuscript characterize new anion conducting that is more red-shifted in its spectrum than prior variants called MsACR1. An additional mutant variant of MsACR1 that is renamed raACR has a 20 nm red-shifted spectral response with faster kinetics. Due to the spectral shift of these variants, the authors proposed that it is possible to inhibit the expression of MsACR1 and raACR with lights at 635 nm in vivo and in vitro. The authors were able to demonstrate some inhibition in vitro and in vivo with 635 nm light. Overall the new variants with unique properties should be able to suppress neuronal activities with red-shifted light stimulation.

Strengths:

The authors were able to identify a new class of anion conducting channelrhodopsin and have variants that respond strongly to lights with wavelength >550 nm. The authors were able to demonstrate this variant, MsACR1, can alter behavior in vivo with 635 nm light. The second major strength of the study is the development of a red-shifted mutant of MsACR1 that has faster kinetics and 20 nm red-shifted from a single mutation.

Weaknesses:

The red-shifted raACR appears to work much less efficiently than MsACR1 even with 635 nm light illumination both in vivo (Figure 4) and in vitro (Figure 3E) despite the 20 nm red-shift. This is inconsistent with the benefits and effects of red-shifting the spectrum in raACR. This usually would suggest raACR either has a lower conductance than MsACR1 or that the membrane/overall expression of raACR is much weaker than MsACR1. Neither of these is measured in the current manuscript.

Thank you for addressing this crucial issue. We posit that the diminished efficiency of raACR in comparison to MsACR1 WT can be attributed to the tenfold acceleration of its photocycle. As noted by Reviewer 1, the anticipated advantages associated with a red-shifted opsin, particularly in in vivo preparations, are offset by its accelerated off-kinetics. Consequently, the shorter dwell time of the open state leads to a reduced number of conducted ions per photon. Nevertheless, the operational light sensitivity is not drastically altered compared to MsACR WT (Fig. 3C). We believe that the rapid kinetics offer interesting applications, such as the precise inhibition of single action potentials through holography.

There are limited comparisons to existing variants of ACRs under the same conditions in the manuscript overall. There should be more parallel comparison with gtACR1, ZipACR, and RubyACR in identical conditions in cultured cell lines, cultured neurons, and in vivo. This should be in terms of overall performance, efficiency, and expression in identical conditions. Without this information, it is unclear whether the effects at 635 nm are due to the expression level which can compensate for the spectral shift.

We compared MsACR1 and raACR with GtACR1 in ND cells in supplemental figure 4. We concur that further comparisons could be useful to emphasise both the strengths of MsACRs and applications where they may not be as suitable. We are currently in the process of outlining a separate article. We firmly believe that each ACR variant occupies a distinct application niche, which necessitates a more comprehensive electrophysiological comparison to provide valuable insights to the scientific community.

There should be more raw traces from the recordings of the different variants in response to short pulse stimulation and long pulse stimulation to different wavelengths. It is difficult to judge what the response would be like when these types of information are missing.

We appreciate Reviewer 1's feedback and have compiled a collection of raw photoresponses, encompassing various pulse widths and wavelengths, which can be found in the Supplementary materials (Supplementary Figures 4 and 5).

Despite being able to activate the channelrhodopsin with 635 nm light, the main utility of the variant should be transcranial stimulation which was not demonstrated here.

We concur with Reviewer 1's assessment that MsACR prime application is indeed transcranial stimulation. However, it's worth emphasising that the full advantages of transcranial optical stimulation become most apparent when animals are truly freely moving without any tethered patch cords. Our ongoing research in the laboratory is dedicated to the development of a wireless LED system that can be securely affixed to the animal's skull. We aim to demonstrate the potential of these novell optogenetic approaches in the field of behavioural neuroscience in the coming year.

Figure 3B is not clearly annotated and is difficult to match the explanation in the figure legend to the figure. The action potential spikings of neurons expressing raACR in this panel are inhibited as strongly as MsACR1.

We have enhanced the figure caption and annotations for clarity. The traces presented in Figure 3B are intended to demonstrate the overall effectiveness of each variant. However, it is in the population data analysis, as depicted in Figure 3E, where the meaningful insights are revealed.

For many characterizations, the number of 'n's are quite low (3-7).

We acknowledge Reviewer 1's suggestion regarding the in vivo data and agree with the importance of including more animals, as well as control animals. However, we are committed to adhering to the principles of the 3Rs (Replacement, Reduction, Refinement) in animal research, and given the robustness of our observed effects, we will add animals to reach the minimal number of animals per condition (n = 2) to minimise unnecessary animal usage while ensuring statistical power.

We will continue to adhere to the established standards in the field, aiming for a range of 3 to 7 cells per condition, sourced from at least two independent preparations, to ensure the robustness and reliability of our in vitro data.

Reviewer #2 (Public Review):

Summary:

The authors identified a new chloride-conducting Channelrhodopsin (MsACR1) that can be activated at low light intensities and within the red part of the visible spectrum. Additional engineering of MsACR1 yielded a variant (raACR1) with increased current amplitudes, accelerated kinetics, and a 20nm red-shifted peak excitation wavelength. Stimulation of MsACR1 and raACR1 expressing neurons with 635nm in mice's primary motor cortices inhibited the animals' locomotion.

Strengths:

The in vitro characterization of the newly identified ACRs is very detailed and confirms the biophysical properties as described by the authors. Notably, the ACRs are very light sensitive and allow for efficient in vitro inhibition of neurons in the nano Watt/mm^2 range. These new ACRs give neuroscientists and cell biologists a new tool to control chloride flux over biological membranes with high temporal and spatial precision. The red-shifted excitation peaks of these ACRs could allow for multiplexed application with blue-light excited optogenetic tools such as cation-conducting channelrhodopsins or green-fluorescent calcium indicators such as GCaMP.

Weaknesses:

The in-vivo characterization of MsACR1 and raACR1 lacks critical control experiments and is, therefore, too preliminary. The experimental conditions differ fundamentally between in vitro and in vivo characterizations. For example, chloride gradients differ within neurons which can weaken inhibition or even cause excitation at synapses, as pointed out by the authors. Notably, the patch pipettes for the in vitro characterization contained low chloride concentrations that might not reflect possible conditions found in the in vivo preparations, i.e., increasing chloride gradients from dendrites to synapses.

We appreciate Reviewer 2’s feedback regarding missing control experiments. We will respond to these concerns in another section of our manuscript, as suggested.

Regarding the chloride gradient, we understand the concerns of Reviewer 2, yet we chose these ionic conditions, particularly as they were used in the initial electrical characterization of GtACR1 in a neuronal context (Mahn et al., 2016). We will make sure to provide this context in our manuscript to justify our choice of ionic conditions.

Interestingly, the authors used soma-targeted (st) MsACR1 and raACR1 for some of their in vitro characterization yielding more efficient inhibition and reduction of co-incidental "on-set" spiking. Still, the authors do not seem to have utilized st-variants in vivo.

At the time of submission, due to the long-term absence of our lab technician, we were not able to produce purified viruses. Therefore, we decided to move on with the submission. We now produced the virus externally, and will provide the experiments.

Most importantly, critical in vivo control experiments, such as negative controls like GFP or positive controls like NpHR, are missing. These controls would exclude potential behavioral effects due to experimental artifacts. Moreover, in vivo electrophysiology could have confirmed whether targeted neurons were inhibited under optogenetic stimulations.

We have several non-injected control animals that we used to calibrate this particular paradigm and never saw similar responses. However, we acknowledge the suggestion of Reviewer 2 and will include the GFP-injected control as recommended.

Some of these concerns stem from the fact that the pulsed raACR stimulation at 635 nm at 10Hz (Fig. 3E) was far less efficient compared to MsACR1, yet the in vivo comparison yielded very similar results (Fig. 4D).

As outlined previously, the accelerated photocycle of raACR results in a reduction in photocurrent amplitude, consequently diminishing the potency of inhibition per photon. In the context of in vitro stimulation, where single action potentials are recorded, this reduction in inhibition efficiency is resolved. However, in the realm of in vivo behavioural analysis, the observed effect is not contingent on single action potentials but rather stems from the disruption of the entire M1 motor network. In this context, despite the reduced efficiency of the fast-cycling raACR, it still manages to interrupt the M1 network, leading to similar behavioural outcomes.

Also, the cortex is highly heterogeneous and comprises excitatory and inhibitory neurons. Using the synapsin promoter, the viral expression paradigm could target both types and cause differential effects, which has not been investigated further, for example, by immunohistochemistry. An alternative expression system, for example, under VGLUT1 control, could have mitigated some of these concerns.

Indeed, we acknowledge the limitations of our current experimental approach. We are in the process of planning and conducting additional experiments involving cre-dependent expression of st-MSACR and st-raACR in PV-Cre mice.

Furthermore, the authors applied different light intensities, wavelengths, and stimulation frequencies during the in vitro characterization, causing varying spike inhibition efficiencies. The in vivo characterization is notably lacking this type of control. Thus, it is unclear why the 635nm, 2s at 20Hz every 5s stimulation protocol, which has no equivalent in the in vitro characterization, was chosen.

We appreciate the valuable comment from the reviewer. The objective of our in vitro characterization is to elucidate the general effects of specific stimulation parameters on the efficiency of neuronal inhibition. For instance, we aim to demonstrate that lower light intensities result in less efficient inhibition, or that pulse stimulation may lead to a less complete inhibition, albeit significantly reducing the energy input into the system.

In the in vivo characterization, we face constraints such as animal welfare considerations and limitations in available laser lines, which prevent us from exploring the entire parameter space as comprehensively as in the in vitro preparation. Additionally, it is important to note that membrane capacitance tends to be higher in vivo compared to dissociated hippocampal neurons. Consequently, we have opted for a doubled stimulation frequency from 10 Hz to 20 Hz and the stimulation pattern of 2 seconds ”on” and 5 seconds “off”. This approach allows the animals to spend less time in an arrested state while still demonstrating the effect of MsACR and variants.

In summary, the in vivo experiments did not confirm whether the observed inhibition of mouse locomotion occurred due to the inhibition of neurons or experimental artifacts.

In addition, the author's main claim of more efficient neuronal inhibition would require them to threshold MsACR1 and raACR1 against alternative methods such as the red-shifted NpHR variant Jaws or other ACRs to give readers meaningful guidance when choosing an inhibitory tool.

The light sensitivity of MsACR1 and raACR1 are impressive and well characterized in vitro. However, the authors only reported the overall light output at the fiber tip for the in vivo experiments: 0.5 mW. Without context, it is difficult to evaluate this value. Calculating the light power density at certain distances from the light fiber or thresholding against alternative tools such as NpHR, Jaws, or other ACRs would allow for a more meaningful evaluation.

We thank the reviewers for their comments.

Reviewer #1 (Recommendations For The Authors):

The study would be much strengthened if the authors can perform more experiments and characterization to support their claims, in addition to showing more raw electrophysiological traces/results and not just summary charts and graphs.

As outlined above, further experiments are planned. We appreciate the suggestion to include more raw electrophysiological traces. Photocurrent traces of all included mutants of MsACR1 measured in ND cells and traces of hippocampal neuronal measurements of non- and soma-targeted MsACR1 and raACR will be included as supplemental figures.

Reviewer #2 (Recommendations For The Authors):

Major concern:

It is unclear if the optogenetic light stimulation in Fig. 4 caused direct inhibition of neuronal activity in M1, which cell types were targeted, and how MsACR1 and raACR1 compare to other optogenetic inhibitors.

Also, the rationale for the light stimulation (635 nm, 2s, 20Hz, every 5s) is not clear.

I would suggest the following to address these concerns:

(1) M1 expression and stimulation of a negative control such as GFP to exclude that experimental artifacts cause the observed behavioral outcomes.

We are now preparing the required GFP control, and will add it to the new version of the manuscript.

(2) Expression and stimulation of NpHR as a positive control.

We will use st-GtACR1 as a positive control.

(3) Electrophysiological measurements of neuronal activity under optogenetic stimulation to confirm the effectiveness of neuronal inhibition, i.e. suppression of spontaneous firing under light etc.

We concur with Reviewer 2 regarding the potential value of incorporating such in vivo optrode recordings into our manuscript to enable readers to assess the effectiveness of MsACR. As part of our plan for the next version of the manuscript, we intend to conduct these experiments.

(4) ChR2 or other cation-conducting channelrhodopsins with the same expression paradigm could be used to observe diametrically opposite effects.

As Reviewer 2 has already pointed out, the complex interactions that can occur in our viral strategy when an inhibitory opsin is expressed in both excitatory and inhibitory neurons make us sceptical about the possibility of an excitatory opsin leading to opposing effects.

Considering the non-linear input-output function of cortical circuits, optogenetic activation of neurons, even when expressed in either inhibitory or excitatory neurons, is likely to result in the perturbation of the cortical network, which will likely also lead to locomotor arrest.

(5) The authors should confirm whether the expression under synapsin preferentially targeted excitatory and inhibitory cells because inhibiting inhibitory cells could lead to the disinhibition of the principal cells. Synapsin promoters can drive expression in glutamatergic and GABAergic neurons. An alternative expression system under VGLUT1 promoter could yield better targeting.

We concur with Reviewer 2 and will conduct the next set of experiments using the PV-Cre mouse line. Additionally, we will employ in vivo electrophysiology to further confirm the inhibition of the motor cortex network.

(6) Titrating of optogenetic stimulation: The author should test whether increasing or decreasing light intensities and stimulation frequencies as well as different wavelengths (550 nm vs 635 nm) cause differences in inhibiting locomotion in vivo as it did for inhibiting the neuronal firing in vitro (Fig. 3B-E).

The non-linear input-output function within cortical networks, coupled with our sole reliance on behaviour as a readout, will pose challenges in resolving subtle effects on locomotion arrest across various stimulation parameters.

For our planned in vivo electrophysiology recordings, we will measure cortical firing rates as a proxy rather than relying solely on behavioural observations. This approach will allow us to map the fundamental axes of our parameter space in vivo, considering factors such as wavelength, light intensity, and frequency

(7) Explanation of why the 20Hz/2s light stimulation protocol was chosen.

As outlined above, considering animal welfare and increased membrane capacitance in vivo, we opted for the outlined stimulation protocol. This approach allows the animals to spend less time in an arrested state while still demonstrating the effect of MsACR and variants.

(8) In vivo thresholding against other inhibitory tools, such as RubyACRs, Jaws, etc would provide critical guidance for the audience and potential users. It would be particularly important to compare the necessary light intensities for reaching similar behavioral outcomes.

We concur with Reviewer 2 and will prepare data using GtACR1 as a reference.

(9) The author should calculate or reasonably estimate the in vivo light intensity during optogenetic stimulation to provide a meaningful comparison to their in vitro characterization. Ideally, they can provide an estimated volume for efficient stimulation of MsACR1 and raACR1 and compare it to other optogenetic tools.

We will conduct a Monte Carlo simulation and offer a comparison of the effective activation volume across various classes of optogenetic tools.

Minor concerns:

(1) Why were st- MsACR1 and raACR1 used in vitro but not in vivo? The viral constructs were described as AAV/DJ-hSyn1-MsACR-mCerulean and AAV/DJ-hSyn1-raACR-mCerulean.

As mentioned earlier, we were unable to produce purified soma-targeted MsACR variants before the manuscript submission. We will now provide these measurements.

(2) Light intensities for the spectral measurements are missing.

During action spectra measurements, a motorised neutral density filter wheel is used to have equal photon flux for all tested wavelengths. Additionally, the light intensity is further reduced by using additional neutral density filters to ensure sufficiently low photocurrents to determine the spectral maximum. Therefore, the light intensity varied between constructs and sometimes measurements. We added the following line to the respective methods section to further clarify this: “(typically in the low µW-range at 𝜆max)”.

(3) MsACR1 is slower and probably more light-sensitive than raACR1, which is faster but has larger photocurrents. These are complementary tradeoffs, and the audience might wonder how MsACR1 and raACR1 photocurrents compare under similar conditions. Therefore, I suggest an alternative representation in Fig. 2C. That is, the presentation of the excitation spectra under similar light intensities and with absolute photocurrent values.

Unfortunately, due to the reasons stated above, MsACR1 and raACR action spectra were not recorded with the same light intensity. However, MsACR1 and raACR are compared under the same conditions for Fig. 2B, E, and F (560 nm light at ~3.2 mW/mm2) as well as in Supp. Fig. 4C.

(4) Figure legends for figures 3F and G are missing details for describing the stimulation paradigm.

We added more details about the stimulation paradigm.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This paper presents a compelling and comprehensive study of decision-making under uncertainty. It addresses a fundamental distinction between belief-based (cognitive neuroscience) formulations of choice behaviour with reward-based (behavioural psychology) accounts. Specifically, it asks whether active inference provides a better account of planning and decision-making, relative to reinforcement learning. To do this, the authors use a simple but elegant paradigm that includes choices about whether to seek both information and rewards. They then assess the evidence for active inference and reinforcement learning models of choice behaviour, respectively. After demonstrating that active inference provides a better explanation of behavioural responses, the neuronal correlates of epistemic and instrumental value (under an optimised active inference model) are characterised using EEG. Significant neuronal correlates of both kinds of value were found in sensor and source space. The source space correlates are then discussed sensibly, in relation to the existing literature on the functional anatomy of perceptual and instrumental decision-making under uncertainty.

Strengths:

The strengths of this work rest upon the theoretical underpinnings and careful deconstruction of the various determinants of choice behaviour using active inference. A particular strength here is that the experimental paradigm is designed carefully to elicit both information-seeking and reward-seeking behaviour; where the information-seeking is itself separated into resolving uncertainty about the context (i.e., latent states) and the contingencies (i.e., latent parameters), under which choices are made. In other words, the paradigm - and its subsequent modelling - addresses both inference and learning as necessary belief and knowledge-updating processes that underwrite decisions.

The authors were then able to model belief updating using active inference and then look for the neuronal correlates of the implicit planning or policy selection. This speaks to a further strength of this study; it provides some construct validity for the modelling of belief updating and decision-making; in terms of the functional anatomy as revealed by EEG. Empirically, the source space analysis of the neuronal correlates licences some discussion of functional specialisation and integration at various stages in the choices and decision-making.

In short, the strengths of this work rest upon a (first) principles account of decision-making under uncertainty in terms of belief updating that allows them to model or fit choice behaviour in terms of Bayesian belief updating - and then use relatively state-of-the-art source reconstruction to examine the neuronal correlates of the implicit cognitive processing.

Response: We are deeply grateful for your careful review of our work and for the thoughtful feedback you have provided. Your dedication to ensuring the quality and clarity of the work is truly admirable. Your comments have been invaluable in guiding us towards improving the paper, and We appreciate your time and effort in not just offering suggestions but also providing specific revisions that I can implement. Your insights have helped us identify areas where I can strengthen the arguments and clarify the methodology.

Comment 1:

The main weaknesses of this report lies in the communication of the ideas and procedures. Although the language is generally excellent, there are some grammatical lapses that make the text difficult to read. More importantly, the authors are not consistent in their use of some terms; for example, uncertainty and information gain are sometimes conflated in a way that might confuse readers. Furthermore, the descriptions of the modelling and data analysis are incomplete. These shortcomings could be addressed in the following way.

First, it would be useful to unpack the various interpretations of information and goal-seeking offered in the (active inference) framework examined in this study. For example, it will be good to include the following paragraph:

"In contrast to behaviourist approaches to planning and decision-making, active inference formulates the requisite cognitive processing in terms of belief updating in which choices are made based upon their expected free energy. Expected free energy can be regarded as a universal objective function, specifying the relative likelihood of alternative choices. In brief, expected free energy can be regarded as the surprise expected following some action, where the expected surprise comes in two flavours. First, the expected surprise is uncertainty, which means that policies with a low expected free energy resolve uncertainty and promote information seeking. However, one can also minimise expected surprise by avoiding surprising, aversive outcomes. This leads to goal-seeking behaviour, where the goals can be regarded as prior preferences or rewarding outcomes.

Technically, expected free energy can be expressed in terms of risk plus ambiguity - or rearranged to be expressed in terms of expected information gain plus expected value, where value corresponds to (log) prior preferences. We will refer to both decompositions in what follows; noting that both decompositions accommodate information and goal-seeking imperatives. That is, resolving ambiguity and maximising information gain have epistemic value, while minimising risk or maximising expected value have pragmatic or instrumental value. These two kinds of values are sometimes referred to in terms of intrinsic and extrinsic value, respectively [1-4]."

Response 1: We deeply thank you for your comments and corresponding suggestions about our interpretations of active inference. In response to your identified weaknesses and suggestions, we have added corresponding paragraphs in the Methods section (The free energy principle and active inference, line 95-106):

“Active inference formulates the necessary cognitive processing as a process of belief updating, where choices depend on agents' expected free energy. Expected free energy serves as a universal objective function, guiding both perception and action. In brief, expected free energy can be seen as the expected surprise following some policies. The expected surprise can be reduced by resolving uncertainty, and one can select policies with lower expected free energy which can encourage information-seeking and resolve uncertainty. Additionally, one can minimize expected surprise by avoiding surprising or aversive outcomes (oudeyer et al., 2007; Schmidhuber et al., 2010). This leads to goal-seeking behavior, where goals can be viewed as prior preferences or rewarding outcomes.

Technically, expected free energy can also be expressed as expected information gain plus expected value, where the value corresponds to (log) prior preferences. We will refer to both formulations in what follows. Resolving ambiguity, minimizing risk, and maximizing information gain has epistemic value while maximizing expected value have pragmatic or instrumental value. These two types of values can be referred to in terms of intrinsic and extrinsic value, respectively (Barto et al., 2013; Schwartenbeck et al., 2019).”

Oudeyer, P. Y., & Kaplan, F. (2007). What is intrinsic motivation? A typology of computational approaches. Frontiers in neurorobotics, 1, 108.

Schmidhuber, J. (2010). Formal theory of creativity, fun, and intrinsic motivation (1990–2010). IEEE transactions on autonomous mental development, 2(3), 230-247.

Barto, A., Mirolli, M., & Baldassarre, G. (2013). Novelty or surprise?. Frontiers in psychology, 4, 61898.

Schwartenbeck, P., Passecker, J., Hauser, T. U., FitzGerald, T. H., Kronbichler, M., & Friston, K. J. (2019). Computational mechanisms of curiosity and goal-directed exploration. elife, 8, e41703.

Comment 2:

The description of the modelling of choice behaviour needs to be unpacked and motivated more carefully. Perhaps along the following lines:

"To assess the evidence for active inference over reinforcement learning, we fit active inference and reinforcement learning models to the choice behaviour of each subject. Effectively, this involved optimising the free parameters of active inference and reinforcement learning models to maximise the likelihood of empirical choices. The resulting (marginal) likelihood was then used as the evidence for each model. The free parameters for the active inference model scaled the contribution of the three terms that constitute the expected free energy (in Equation 6). These coefficients can be regarded as precisions that characterise each subjects' prior beliefs about contingencies and rewards. For example, increasing the precision or the epistemic value associated with model parameters means the subject would update her beliefs about reward contingencies more quickly than a subject who has precise prior beliefs about reward distributions. Similarly, subjects with a high precision over prior preferences or extrinsic value can be read as having more precise beliefs that she will be rewarded. The free parameters for the reinforcement learning model included..."

Response 2: We deeply thank you for your comments and corresponding suggestions about our description of the behavioral modelling. In response to your identified weaknesses and suggestions, we have added corresponding content in the Results section (Behavioral results, line 279-293):

“To assess the evidence for active inference over reinforcement learning, we fit active inference (Eq.9), model-free reinforcement learning, and model-based reinforcement learning models to the behavioral data of each participant. This involved optimizing the free parameters of active inference and reinforcement learning models. The resulting likelihood was used to calculate the Bayesian Information Criterion (BIC) (Vrieze 2012) as the evidence for each model. The free parameters for the active inference model (AL, AI, EX, prior, and α) scaled the contribution of the three terms that constitute the expected free energy in Eq.9. These coefficients can be regarded as precisions that characterize each participant's prior beliefs about contingencies and rewards. For example, increasing α means participants would update their beliefs about reward contingencies more quickly, increasing AL means participants would like to reduce ambiguity more, and increasing AI means participants would like to learn the hidden state of the environment and avoid risk more. The free parameters for the model-free reinforcement learning model are the learning rate α and the temperature parameter γ and the free parameters for the model-based are the learning rate α, the temperature parameter γ and prior (the details for the model-free reinforcement learning model can be seen in Eq.S1-11 and the details for the model-based reinforcement learning model can be seen Eq.S12-23 in the Supplementary Method). The parameter fitting for these three models was conducted using the `BayesianOptimization' package in Python (Frazire 2018), first randomly sampling 1000 times and then iterating for an additional 1000 times.”

Vrieze, S. I. (2012). Model selection and psychological theory: a discussion of the differences between the Akaike information criterion (AIC) and the Bayesian information criterion (BIC). Psychological methods, 17(2), 228.

Frazier, P. I. (2018). A tutorial on Bayesian optimization. arXiv preprint arXiv:1807.02811.

Comment 3:

In terms of the time-dependent correlations with expected free energy - and its constituent terms - I think the report would benefit from overviewing these analyses with something like the following:

"In the final analysis of the neuronal correlates of belief updating - as quantified by the epistemic and intrinsic values of expected free energy - we present a series of analyses in source space. These analyses tested for correlations between constituent terms in expected free energy and neuronal responses in source space. These correlations were over trials (and subjects). Because we were dealing with two-second timeseries, we were able to identify the periods of time during decision-making when the correlates were expressed.

In these analyses, we focused on the induced power of neuronal activity at each point in time, at each brain source. To illustrate the functional specialisation of these neuronal correlates, we present whole-brain maps of correlation coefficients and pick out the most significant correlation for reporting fluctuations in selected correlations over two-second periods. These analyses are presented in a descriptive fashion to highlight the nature and variety of the neuronal correlates, which we unpack in relation to the existing EEG literature in the discussion. Note that we did not attempt to correct for multiple comparisons; largely, because the correlations observed were sustained over considerable time periods, which would be almost impossible under the null hypothesis of no correlations."

Response 3: We deeply thank you for your comments and corresponding suggestions about our description of the regression analysis in the source space. In response to your suggestions, we have added corresponding content in the Results section (EEG results at source level, line 331-347):

“In the final analysis of the neural correlates of the decision-making process, as quantified by the epistemic and intrinsic values of expected free energy, we presented a series of linear regressions in source space. These analyses tested for correlations over trials between constituent terms in expected free energy (the value of avoiding risk, the value of reducing ambiguity, extrinsic value, and expected free energy itself) and neural responses in source space. Additionally, we also investigated the neural correlate of (the degree of) risk, (the degree of) ambiguity, and prediction error. Because we were dealing with a two-second time series, we were able to identify the periods of time during decision-making when the correlates were expressed. The linear regression was run by the "mne.stats.linear regression" function in the MNE package (Activity ~ Regressor + Intercept). Activity is the activity amplitude of the EEG signal in the source space and regressor is one of the regressors that we mentioned (e.g., expected free energy, the value of reducing ambiguity, etc.).

In these analyses, we focused on the induced power of neural activity at each time point, in the brain source space. To illustrate the functional specialization of these neural correlates, we presented whole-brain maps of correlation coefficients and picked out the brain region with the most significant correlation for reporting fluctuations in selected correlations over two-second periods. These analyses were presented in a descriptive fashion to highlight the nature and variety of the neural correlates, which we unpacked in relation to the existing EEG literature in the discussion. Note that we did not attempt to correct for multiple comparisons; largely, because the correlations observed were sustained over considerable time periods, which would be almost impossible under the null hypothesis of no correlations.”

Comment 4:

There was a slight misdirection in the discussion of priors in the active inference framework. The notion that active inference requires a pre-specification of priors is a common misconception. Furthermore, it misses the point that the utility of Bayesian modelling is to identify the priors that each subject brings to the table. This could be easily addressed with something like the following in the discussion:

"It is a common misconception that Bayesian approaches to choice behaviour (including active inference) are limited by a particular choice of priors. As illustrated in our fitting of choice behaviour above, priors are a strength of Bayesian approaches in the following sense: under the complete class theorem [5, 6], any pair of choice behaviours and reward functions can be described in terms of ideal Bayesian decision-making with particular priors. In other words, there always exists a description of choice behaviour in terms of some priors. This means that one can, in principle, characterise any given behaviour in terms of the priors that explain that behaviour. In our example, these were effectively priors over the precision of various preferences or beliefs about contingencies that underwrite expected free energy."

Response 4: We deeply thank you for your comments and corresponding suggestions about the prior of Bayesian methods. In response to your suggestions, we have added corresponding content in the Discussion section (The strength of the active inference framework in decision-making, line 447-453):

“However, it may be the opposite. As illustrated in our fitting results, priors can be a strength of Bayesian approaches. Under the complete class theorem (Wald 1947; Brown 1981), any pair of behavioral data and reward functions can be described in terms of ideal Bayesian decision-making with particular priors. In other words, there always exists a description of behavioral data in terms of some priors. This means that one can, in principle, characterize any given behavioral data in terms of the priors that explain that behavior. In our example, these were effectively priors over the precision of various preferences or beliefs about contingencies that underwrite expected free energy.”

Wald, A. (1947). An essentially complete class of admissible decision functions. The Annals of Mathematical Statistics, 549-555.

Brown, L. D. (1981). A complete class theorem for statistical problems with finite sample spaces. The Annals of Statistics, 1289-1300.

Reviewer #2 (Public Review):

Summary:

Zhang and colleagues use a combination of behavioral, neural, and computational analyses to test an active inference model of exploration in a novel reinforcement learning task.

Strengths:

The paper addresses an important question (validation of active inference models of exploration). The combination of behavior, neuroimaging, and modeling is potentially powerful for answering this question.

Response: We want to express our sincere gratitude for your thorough review of our work and for the valuable comments you have provided. Your attention to detail and dedication to improving the quality of the work are truly commendable. Your feedback has been invaluable in guiding us towards revisions that will strengthen the work. We have made targeted modifications based on most of the comments. However, due to factors such as time and energy constraints, we have not added corresponding analyses for several comments.

Comment 1:

The paper does not discuss relevant work on contextual bandits by Schulz, Collins, and others. It also does not mention the neuroimaging study of Tomov et al. (2020) using a risky/safe bandit task.

Response 1:

We deeply thank you for your suggestions about the relevant work. We now discussion and cite these representative papers in the Introduction section (line 42-55):

“The decision-making process frequently involves grappling with varying forms of uncertainty, such as ambiguity - the kind of uncertainty that can be reduced through sampling, and risk - the inherent uncertainty (variance) presented by a stable environment. Studies have investigated these different forms of uncertainty in decision-making, focusing on their neural correlates (Daw et al., 2006; Badre et al., 2012; Cavanagh et al., 2012).

These studies utilized different forms of multi-armed bandit tasks, e.g the restless multi-armed bandit tasks (Daw et al., 2006; Guha et al., 2010), risky/safe bandit tasks (Tomov et al., 2020; Fan et al., 2022; Payzan et al., 2013), contextual multi-armed bandit tasks (Schulz et al., 2015; Schulz et al., 2015; Molinaro et al., 2023). However, these tasks either separate risk from ambiguity in uncertainty, or separate action from state (perception). In our work, we develop a contextual multi-armed bandit task to enable participants to actively reduce ambiguity, avoid risk, and maximize rewards using various policies (see Section 2.2) and Figure 4(a)). Our task makes it possible to study whether the brain represents these different types of uncertainty distinctly (Levy et al., 2010) and whether the brain represents both the value of reducing uncertainty and the degree of uncertainty. The active inference framework presents a theoretical approach to investigate these questions. Within this framework, uncertainties can be reduced to ambiguity and risk. Ambiguity is represented by the uncertainty about model parameters associated with choosing a particular action, while risk is signified by the variance of the environment's hidden states. The value of reducing ambiguity, the value of avoiding risk, and extrinsic value together constitute expected free energy (see Section 2.1).”

Daw, N. D., O'doherty, J. P., Dayan, P., Seymour, B., & Dolan, R. J. (2006). Cortical substrates for exploratory decisions in humans. Nature, 441(7095), 876-879.

Badre, D., Doll, B. B., Long, N. M., & Frank, M. J. (2012). Rostrolateral prefrontal cortex and individual differences in uncertainty-driven exploration. Neuron, 73(3), 595-607.

Cavanagh, J. F., Figueroa, C. M., Cohen, M. X., & Frank, M. J. (2012). Frontal theta reflects uncertainty and unexpectedness during exploration and exploitation. Cerebral cortex, 22(11), 2575-2586.

Guha, S., Munagala, K., & Shi, P. (2010). Approximation algorithms for restless bandit problems. Journal of the ACM (JACM), 58(1), 1-50.

Tomov, M. S., Truong, V. Q., Hundia, R. A., & Gershman, S. J. (2020). Dissociable neural correlates of uncertainty underlie different exploration strategies. Nature communications, 11(1), 2371.

Fan, H., Gershman, S. J., & Phelps, E. A. (2023). Trait somatic anxiety is associated with reduced directed exploration and underestimation of uncertainty. Nature Human Behaviour, 7(1), 102-113.

Payzan-LeNestour, E., Dunne, S., Bossaerts, P., & O’Doherty, J. P. (2013). The neural representation of unexpected uncertainty during value-based decision making. Neuron, 79(1), 191-201.

Schulz, E., Konstantinidis, E., & Speekenbrink, M. (2015, April). Exploration-exploitation in a contextual multi-armed bandit task. In International conference on cognitive modeling (pp. 118-123).

Schulz, E., Konstantinidis, E., & Speekenbrink, M. (2015, November). Learning and decisions in contextual multi-armed bandit tasks. In CogSci.

Molinaro, G., & Collins, A. G. (2023). Intrinsic rewards explain context-sensitive valuation in reinforcement learning. PLoS Biology, 21(7), e3002201.

Levy, I., Snell, J., Nelson, A. J., Rustichini, A., & Glimcher, P. W. (2010). Neural representation of subjective value under risk and ambiguity. Journal of neurophysiology, 103(2), 1036-1047.

Comment 2:

The statistical reporting is inadequate. In most cases, only p-values are reported, not the relevant statistics, degrees of freedom, etc. It was also not clear if any corrections for multiple comparisons were applied. Many of the EEG results are described as "strong" or "robust" with significance levels of p<0.05; I am skeptical in the absence of more details, particularly given the fact that the corresponding plots do not seem particularly strong to me.

Response 2: We deeply thank you for your comments about our statistical reporting. We have optimized the fitting model and rerun all the statistical analyses. As can be seen (Figure 6, 7, 8, S3, S4, S5), the new regression results are significantly improved compared to the previous ones. Due to the limitation of space, we place the other relevant statistical results, including t-values, std err, etc., on our GitHub (https://github.com/andlab-um/FreeEnergyEEG). Currently, we have not conducted multiple comparison corrections based on Reviewer 1’s comments (Comments 3) “Note that we did not attempt to correct for multiple comparisons; largely, because the correlations observed were sustained over considerable time periods, which would be almost impossible under the null hypothesis of no correlations”.

Author response image 1.

Comment 3:

The authors compare their active inference model to a "model-free RL" model. This model is not described anywhere, as far as I can tell. Thus, I have no idea how it was fit, how many parameters it has, etc. The active inference model fitting is also not described anywhere. Moreover, you cannot compare models based on log-likelihood, unless you are talking about held-out data. You need to penalize for model complexity. Finally, even if active inference outperforms a model-free RL model (doubtful given the error bars in Fig. 4c), I don't see how this is strong evidence for active inference per se. I would want to see a much more extensive model comparison, including model-based RL algorithms which are not based on active inference, as well as model recovery analyses confirming that the models can actually be distinguished on the basis of the experimental data.

Response 3: We deeply thank you for your comments about the model comparison details. We previously omitted some information about the comparison model, as classical reinforcement learning is not the focus of our work, so we put the specific details in the supplementary materials. Now we have placed relevant information in the main text (see the part we have highlighted in yellow). We have now added the relevant information regarding the model comparison in the Results section (Behavioral results, line 279-293):

“To assess the evidence for active inference over reinforcement learning, we fit active inference (Eq.9), model-free reinforcement learning, and model-based reinforcement learning models to the behavioral data of each participant. This involved optimizing the free parameters of active inference and reinforcement learning models. The resulting likelihood was used to calculate the Bayesian Information Criterion (BIC) as the evidence for each model. The free parameters for the active inference model (AL, AI, EX, prior, and α) scaled the contribution of the three terms that constitute the expected free energy in Eq.9. These coefficients can be regarded as precisions that characterize each participant's prior beliefs about contingencies and rewards. For example, increasing α means participants would update their beliefs about reward contingencies more quickly, increasing AL means participants would like to reduce ambiguity more, and increasing AI means participants would like to learn the hidden state of the environment and avoid risk more. The free parameters for the model-free reinforcement learning model are the learning rate α and the temperature parameter γ and the free parameters for the model-based are the learning rate α, the temperature parameter γ and prior (the details for the model-free reinforcement learning model can be found in Eq.S1-11 and the details for the model-based reinforcement learning model can be found in Eq.S12-23 in the Supplementary Method). The parameter fitting for these three models was conducted using the `BayesianOptimization' package in Python, first randomly sampling 1000 times and then iterating for an additional 1000 times.”

We have now incorporated model-based reinforcement learning into our comparison models and placed the descriptions of both model-free and model-based reinforcement learning algorithms in the supplementary materials. We have also changed the criterion for model comparison to Bayesian Information Criterion. As indicated by the results, the performance of the active inference model significantly outperforms both comparison models.

Sorry, we didn't do model recovery before, but now we have placed the relevant results in the supplementary materials. From the result figures, we can see that each model fits its own generated simulated data well:

“To demonstrate how reliable our models are (the active inference model, model-free reinforcement learning model, and model-based reinforcement learning model), we run some simulation experiments for model recovery. We use these three models, with their own fitting parameters, to generate some simulated data. Then we will fit all three sets of data using these three models.

The model recovery results are shown in Fig.S6. This is the confusion matrix of models: the percentage of all subjects simulated based on a certain model that is fitted best by a certain model. The goodness-of-fit was compared using the Bayesian Information Criterion. We can see that the result of model recovery is very good, and the simulated data generated by a model can be best explained by this model.”

Author response image 2.

Comment 4:

Another aspect of the behavioral modeling that's missing is a direct descriptive comparison between model and human behavior, beyond just plotting log-likelihoods (which are a very impoverished measure of what's going on).

Response 4: We deeply thank you for your comments about the comparison between the model and human behavior. Due to the slight differences between our simulation experiments and real behavioral experiments (the "you can ask" stage), we cannot directly compare the model and participants' behaviors. However, we can observe that in the main text's simulation experiment (Figure 3), the active inference agent's behavior is highly consistent with humans (Figure 4), exhibiting an effective exploration strategy and a desire to reduce uncertainty. Moreover, we have included two additional simulation experiments in the supplementary materials, which demonstrate that active inference may potentially fit a wide range of participants' behavioral strategies.

Author response image 3.

(An active inference agent with AL=AI=EX=0. It can accomplish tasks efficiently like a human being, reducing the uncertainty of the environment and maximizing the reward.)

Author response image 4.

(An active inference agent with AL=AI=0, EX=10. It will only pursue immediate rewards (not choosing the "Cue" option due to additional costs), but it can also gradually optimize its strategy due to random effects.)

Author response image 5.

(An active inference agent with EX=0, AI=AL=10. It will only pursue environmental information to reduce the uncertainty of the environment. Even in "Context 2" where immediate rewards are scarce, it will continue to explore.)

Figure (a) shows the decision-making of active inference agents in the Stay-Cue choice. Blue corresponds to agents choosing the "Cue" option and acquiring "Context 1"; orange corresponds to agents choosing the "Cue" option and acquiring "Context 2"; purple corresponds to agents choosing the "Stay" option and not knowing the information about the hidden state of the environment. The shaded areas below correspond to the probability of the agents making the respective choices.

Figure (b) shows the decision-making of active inference agents in the Stay-Cue choice. The shaded areas below correspond to the probability of the agents making the respective choices.

Figure (c) shows the rewards obtained by active inference agents.

Figure (d) shows the reward prediction errors of active inference agents.

Figure (e) shows the reward predictions of active inference agents for the "Risky" path in "Context 1" and "Context 2".

Comment 5:

The EEG results are intriguing, but it wasn't clear that these provide strong evidence specifically for the active inference model. No alternative models of the EEG data are evaluated.

Overall, the central claim in the Discussion ("we demonstrated that the active inference model framework effectively describes real-world decision-making") remains unvalidated in my opinion.

Response 5: We deeply thank you for your comments. We applied the active inference model to analyze EEG results because it best fit the participants' behavioral data among our models, including the new added results. Further, our EEG results serve only to verify that the active inference model can be used to analyze the neural mechanisms of decision-making in uncertain environments (if possible, we could certainly design a more excellent reinforcement learning model with a similar exploration strategy). We aim to emphasize the consistency between active inference and human decision-making in uncertain environments, as we have discussed in the article. Active inference emphasizes both perception and action, which is also what we wish to highlight: during the decision-making process, participants not only passively receive information, but also actively adopt different strategies to reduce uncertainty and maximize rewards.

Reviewer #3 (Public Review):

Summary:

This paper aims to investigate how the human brain represents different forms of value and uncertainty that participate in active inference within a free-energy framework, in a two-stage decision task involving contextual information sampling, and choices between safe and risky rewards, which promotes a shift from exploration to exploitation. They examine neural correlates by recording EEG and comparing activity in the first vs second half of trials and between trials in which subjects did and did not sample contextual information, and perform a regression with free-energy-related regressors against data "mapped to source space." Their results show effects in various regions, which they take to indicate that the brain does perform this task through the theorised active inference scheme.

Strengths:

This is an interesting two-stage paradigm that incorporates several interesting processes of learning, exploration/exploitation, and information sampling. Although scalp/brain regions showing sensitivity to the active-inference-related quantities do not necessarily suggest what role they play, it can be illuminating and useful to search for such effects as candidates for further investigation. The aims are ambitious, and methodologically it is impressive to include extensive free-energy theory, behavioural modelling, and EEG source-level analysis in one paper.

Response: We would like to express our heartfelt thanks to you for carefully reviewing our work and offering insightful feedback. Your attention to detail and commitment to enhancing the overall quality of our work are deeply admirable. Your input has been extremely helpful in guiding us through the necessary revisions to enhance the work. We have implemented focused changes based on a majority of your comments. Nevertheless, owing to limitations such as time and resources, we have not included corresponding analyses for a few comments.

Comment 1:

Though I could surmise the above general aims, I could not follow the important details of what quantities were being distinguished and sought in the EEG and why. Some of this is down to theoretical complexity - the dizzying array of constructs and terms with complex interrelationships, which may simply be part and parcel of free-energy-based theories of active inference - but much of it is down to missing or ambiguous details.

Response 1: We deeply thank you for your comments about our work’s readability. We have significantly revised the descriptions of active inference, models, research questions, etc. Focusing on active inference and the free energy principle, we have added relevant basic descriptions and unified the terminology. We have added information related to model comparison in the main text and supplementary materials. We presented our regression results in clearer language. Our research focused on the brain's representation of decision-making in uncertain environments, including expected free energy, the value of reducing ambiguity, the value of avoiding risk, extrinsic value, ambiguity, and risk.

Comment 2:

In general, an insufficient effort has been made to make the paper accessible to readers not steeped in the free energy principle and active inference. There are critical inconsistencies in key terminology; for example, the introduction states that aim 1 is to distinguish the EEG correlates of three different types of uncertainty: ambiguity, risk, and unexpected uncertainty. But the abstract instead highlights distinctions in EEG correlates between "uncertainty... and... risk" and between "expected free energy .. and ... uncertainty." There are also inconsistencies in mathematical labelling (e.g. in one place 'p(s|o)' and 'q(s)' swap their meanings from one sentence to the very next).

Response 2: We deeply thank you for your comments about the problem of inconsistent terminology. First, we have unified the symbols and letters (P, Q, s, o, etc.) that appeared in the article and described their respective meanings more clearly. We have also revised the relevant expressions of "uncertainty" throughout the text. In our work, uncertainty refers to ambiguity and risk. Ambiguity can be reduced through continuous sampling and is referred to as uncertainty about model parameters in our work. Risk, on the other hand, is the inherent variance of the environment and cannot be reduced through sampling, which is referred to as uncertainty about hidden states in our work. In the analysis of the results, we focused on how the brain encodes the value of reducing ambiguity (Figure 8), the value of avoiding risk (Figure 6), and (the degree of) ambiguity (Figure S5) during action selection. We also analyzed how the brain encodes reducing ambiguity and avoiding risk during belief update (Figure 7).

Comment 3:

Some basic but important task information is missing, and makes a huge difference to how decision quantities can be decoded from EEG. For example:

- How do the subjects press the left/right buttons - with different hands or different fingers on the same hand?

Response 3: We deeply thank you for your comments about the missing task information. We have added the relevant content in the Methods section (Contextual two-armed bandit task and Data collection, line 251-253):

“Each stage was separated by a jitter ranging from 0.6 to 1.0 seconds. The entire experiment consists of a single block with a total of 120 trials. The participants are required to use any two fingers of one hand to press the buttons (left arrow and right arrow on the keyboard).”

Comment 4:

- Was the presentation of the Stay/cue and safe/risky options on the left/right sides counterbalanced? If not, decisions can be formed well in advance especially once a policy is in place.

Response 4: The presentation of the Stay/cue and safe/risky options on the left/right sides was not counterbalanced. It is true that participants may have made decisions ahead of time. However, to better study the state of participants during decision-making, our choice stages consist of two parts. In the first two seconds, we ask participants to consider which option they would choose, and after these two seconds, participants are allowed to make their choice (by pressing the button).

We also updated the figure of the experiment procedure as below (We circled the time that the participants spent on making decisions).

Author response image 6.

Comment 5:

- What were the actual reward distributions ("magnitude X with probability p, magnitude y with probability 1-p") in the risky option?

Response 5: We deeply thank you for your comments about the missing task information. We have placed the relevant content in the Methods section (Contextual two-armed bandit task and Data collection, line 188-191):

“The actual reward distribution of the risky path in "Context 1" was [+12 (55%), +9 (25%), +6 (10%), +3 (5%), +0 (5%)] and the actual reward distribution of the risky path in "Context 2" was [+12 (5%), +9 (5%), +6 (10%), +3 (25%), +0 (55%)].”

Comment 6:

The EEG analysis is not sufficiently detailed and motivated.

For example,

- why the high lower-filter cutoff of 1 Hz, and shouldn't it be acknowledged that this removes from the EEG any sustained, iteratively updated representation that evolves with learning across trials?

Response 6: We deeply thank you for your comments about our EEG analysis. The 1Hz high-pass filter may indeed filter out some useful information. We chose a 1Hz high-pass filter to filter out most of the noise and prevent the noise from affecting our results analysis. Additionally, there are also many decision-related works that have applied 1Hz high-pass filtering in EEG data preprocessing (Yau et al., 2021; Cortes et al., 2021; Wischnewski et al., 2022; Schutte et al., 2017; Mennella et al., 2020; Giustiniani et al., 2020).

Yau, Y., Hinault, T., Taylor, M., Cisek, P., Fellows, L. K., & Dagher, A. (2021). Evidence and urgency related EEG signals during dynamic decision-making in humans. Journal of Neuroscience, 41(26), 5711-5722.

Cortes, P. M., García-Hernández, J. P., Iribe-Burgos, F. A., Hernández-González, M., Sotelo-Tapia, C., & Guevara, M. A. (2021). Temporal division of the decision-making process: An EEG study. Brain Research, 1769, 147592.

Wischnewski, M., & Compen, B. (2022). Effects of theta transcranial alternating current stimulation (tACS) on exploration and exploitation during uncertain decision-making. Behavioural Brain Research, 426, 113840.

Schutte, I., Kenemans, J. L., & Schutter, D. J. (2017). Resting-state theta/beta EEG ratio is associated with reward-and punishment-related reversal learning. Cognitive, Affective, & Behavioral Neuroscience, 17, 754-763.

Mennella, R., Vilarem, E., & Grèzes, J. (2020). Rapid approach-avoidance responses to emotional displays reflect value-based decisions: Neural evidence from an EEG study. NeuroImage, 222, 117253.

Giustiniani, J., Nicolier, M., Teti Mayer, J., Chabin, T., Masse, C., Galmès, N., ... & Gabriel, D. (2020). Behavioral and neural arguments of motivational influence on decision making during uncertainty. Frontiers in Neuroscience, 14, 583.

Comment 7:

- Since the EEG analysis was done using an array of free-energy-related variables in a regression, was multicollinearity checked between these variables?

Response 7: We deeply thank you for your comments about our regression. Indeed, we didn't specify our regression formula in the main text. We conducted regression on one variable each time, so there was no need for a multicollinearity check. We have now added the relevant content in the Results section (“EEG results at source level” section, line 337-340):

“The linear regression was run by the "mne.stats.linear regression" function in the MNE package (Activity ~ Regressor + Intercept). Activity is the activity amplitude of the EEG signal in the source space and regressor is one of the regressors that we mentioned (e.g., expected free energy, the value of reducing ambiguity, etc.).”

Comment 8:

- In the initial comparison of the first/second half, why just 5 clusters of electrodes, and why these particular clusters?

Response 8: We deeply thank you for your comments about our sensor-level analysis. These five clusters are relatively common scalp EEG regions to analyze (left frontal, right frontal, central, left parietal, and right parietal), and we referred previous work analyzed these five clusters of electrodes (Laufs et al., 2006; Ray et al., 1985; Cole et al., 1985). In addition, our work pays more attention to the analysis in source space, exploring the corresponding functions of specific brain regions based on active inference models.

Laufs, H., Holt, J. L., Elfont, R., Krams, M., Paul, J. S., Krakow, K., & Kleinschmidt, A. (2006). Where the BOLD signal goes when alpha EEG leaves. Neuroimage, 31(4), 1408-1418.

Ray, W. J., & Cole, H. W. (1985). EEG activity during cognitive processing: influence of attentional factors. International Journal of Psychophysiology, 3(1), 43-48.

Cole, H. W., & Ray, W. J. (1985). EEG correlates of emotional tasks related to attentional demands. International Journal of Psychophysiology, 3(1), 33-41.

Comment 9:

How many different variables are systematically different in the first vs second half, and how do you rule out less interesting time-on-task effects such as engagement or alertness? In what time windows are these amplitudes being measured?

Response 9 (and the Response for Weaknesses 11): There were no systematic differences between the first half and the second half of the trials, with the only difference being the participants' experience. In the second half, participants had a better understanding of the reward distribution of the task (less ambiguity). The simulation results can well describe these.

Author response image 7.

As shown in Figure (a), agents can only learn about the hidden state of the environment ("Context 1" (green) or "Context 2" (orange)) by choosing the "Cue" option. If agents choose the "Stay" option, they will not be able to know the hidden state of the environment (purple). The risk of agents is only related to wh

ether they choose the "Cue" option, not the number of rounds. Figure (b) shows the Safe-Risky choices of agents, and Figure (e) is the reward prediction of agents for the "Risky" path in "Context 1" and "Context 2". We can see that agents update the expected reward and reduce ambiguity by sampling the "Risky" path. The ambiguity of agents is not related to the "Cue" option, but to the number of times they sample the "Risky" path (rounds).

In our choosing stages, participants were required to think about their choices for the first two seconds (during which they could not press buttons). Then, they were asked to make their choices (press buttons) within the next two seconds. This setup effectively kept participants' attention focused on the task. And the two second during the “Second choice” stage when participants decide which option to choose (they cannot press buttons) are measured for the analysis of the sensor-level results.

Comment 10:

In the comparison of asked and not-asked trials, what trial stage and time window is being measured?

Response 10: We have added relevant descriptions in the main text. The two second during the “Second choice” stage when participants decide which option to choose (they cannot press buttons) are measured for the analysis of the sensor-level results.

Author response image 8.

Comment 11:

Again, how many different variables, of the many estimated per trial in the active inference model, are different in the asked and not-asked trials, and how can you know which of these differences is the one reflected in the EEG effects?

Response 11: The difference between asked trials and not-asked trials lies only in whether participants know the specific context of the risky path (the level of risk for the participants). A simple comparison indeed cannot tell us which of these differences is reflected in the EEG effects. Therefore, we subsequently conducted model-based regression analysis in the source space.

Comment 12:

The authors choose to interpret that on not-asked trials the subjects are more uncertain because the cue doesn't give them the context, but you could equally argue that they don't ask because they are more certain of the possible hidden states.

Response 12: Our task design involves randomly varying the context of the risky path. Only by choosing to inquire can participants learn about the context. Participants can only become increasingly certain about the reward distribution of different contexts of the risky path, but cannot determine which specific context it is. Here are the instructions for the task that we will tell the participants (line 226-231).

"You are on a quest for apples in a forest, beginning with 5 apples. You encounter two paths: 1) The left path offers a fixed yield of 6 apples per excursion. 2) The right path offers a probabilistic reward of 0/3/6/9/12 apples, and it has two distinct contexts, labeled "Context 1" and "Context 2," each with a different reward distribution. Note that the context associated with the right path will randomly change in each trial. Before selecting a path, a ranger will provide information about the context of the right path ("Context 1" or "Context 2") in exchange for an apple. The more apples you collect, the greater your monetary reward will be."

Comment 13:

- The EEG regressors are not fully explained. For example, an "active learning" regressor is listed as one of the 4 at the beginning of section 3.3, but it is the first mention of this term in the paper and the term does not arise once in the methods.

Response 13: We have accordingly revised the relevant content in the main text (as in Eq.8). Our regressors now include expected free energy, the value of reducing ambiguity, the value of avoiding risk, extrinsic value, prediction error, (the degree of) ambiguity, reducing ambiguity, and avoiding risk.

Comment 14:

- In general, it is not clear how one can know that the EEG results reflect that the brain is purposefully encoding these very parameters while implementing this very mechanism, and not other, possibly simpler, factors that correlate with them since there is no engagement with such potential confounds or alternative models. For example, a model-free reinforcement learning model is fit to behaviour for comparison. Why not the EEG?

Response 14: We deeply thank you for your comments. Due to factors such as time and effort, and because the active inference model best fits the behavioral data of the participants, we did not use other models to analyze the EEG data. At both the sensor and source level, we observed the EEG signal and brain regions that can encode different levels of uncertainties (risk and ambiguity). The brain's uncertainty driven exploration mechanism cannot be explained solely by a simple model-free reinforcement learning approach.

Recommendations for the authors:

Response: We have made point-to-point revisions according to the reviewer's recommendations, and as these revisions are relatively minor, we have only responded to the longer recommendations here.

Reviewer #1 (Recommendations For The Authors)

I enjoyed reading this sophisticated study of decision-making. I thought your implementation of active inference and the subsequent fitting to choice behaviour - and study of the neuronal (EEG) correlates - was impressive. As noted in my comments on strengths and weaknesses, some parts of your manuscript with difficult to read because of slight collapses in grammar and an inconsistent use of terms when referring to the mathematical quantities. In addition to the paragraphs I have suggested, I would recommend the following minor revisions to your text. In addition, you will have to fill in some of the details that were missing from the current version of the manuscript. For example:

Recommendation 1:

Which RL model did you use to fit the behavioural data? What were its free parameters?

Response 1: We have now added information related to the comparison models in the behavioral results and supplementary materials. We applied both simple model-free reinforcement learning and model-based reinforcement learning. The free parameters for the model-free reinforcement learning model are the learning rate α and the temperature parameter γ, while the free parameters for the model-based approach are the learning rate α, the temperature parameter γ, and the prior.

Recommendation 2:

When you talk about neuronal activity in the final analyses (of time-dependent correlations) what was used to measure the neuronal activity? Was this global power over frequencies? Was it at a particular frequency band? Was it the maximum amplitude within some small window et cetera? In other words, you need to provide the details of your analysis that would enable somebody to reproduce your study at a certain level of detail.

Response 2: In the final analyses, we used the activity amplitude at each point in the source space for our analysis. Previously, we had planned to make our data and models available on GitHub to facilitate easier replication of our work.

Reviewer #3 (Recommendations For The Authors)

Recommendation 1:

It might help to explain the complex concepts up front, to use the concrete example of the task itself - presumably, it was designed so that the crucial elements of the active inference framework come to the fore. One could use hypothetical choice patterns in this task to exemplify different factors such as expected free energy and unexpected uncertainty at work. It would also be illuminating to explain why behaviour on this task is fit better by the active inference model than a model-free reinforcement learning model.

Response 1: Thank you for your suggestions. We have given clearer explanations to the three terms in the active inference formula: the value of reducing ambiguity, the value of avoiding risk, and the extrinsic value (Eq.8), which makes it easier for readers to understand active inference.

In addition, we can simply view active inference as a computational model similar to model-based reinforcement learning, where the expected free energy represents a subjective value, without needing to understand its underlying computational principles or neurobiological background. In our discussion, we have argued why the active inference model fits the participants' behavior better than our reinforcement learning model, as the active inference model has an inherent exploration mechanism that is consistent with humans, who instinctively want to reduce environmental uncertainty (line 435-442).

“Active inference offers a superior exploration mechanism compared with basic model-free reinforcement learning  (Figure 4 (c)). Since traditional reinforcement learning models determine their policies solely on the state, this setting leads to difficulty in extracting temporal information (Laskin et al., 2020) and increases the likelihood of entrapment within local minima. In contrast, the policies in active inference are determined by both time and state. This dependence on time (Wang et al., 2016) enables policies to adapt efficiently, such as emphasizing exploration in the initial stages and exploitation later on. Moreover, this mechanism prompts more exploratory behavior in instances of state ambiguity. A further advantage of active inference lies in its adaptability to different task environments (Friston et al., 2017). It can configure different generative models to address distinct tasks, and compute varied forms of free energy and expected free energy.”

Laskin, M., Lee, K., Stooke, A., Pinto, L., Abbeel, P., & Srinivas, A. (2020). Reinforcement learning with augmented data. Advances in neural information processing systems, 33, 19884-19895.

Wang, J. X., Kurth-Nelson, Z., Tirumala, D., Soyer, H., Leibo, J. Z., Munos, R., ... & Botvinick, M. (2016). Learning to reinforcement learn. arXiv preprint arXiv:1611.05763.

Friston, K., FitzGerald, T., Rigoli, F., Schwartenbeck, P., & Pezzulo, G. (2017). Active inference: a process theory. Neural computation, 29(1), 1-49.

Recommendation 2:

Figure 1A provides a key example of the lack of effort to help the reader understand. It suggests the possibility of a concrete example but falls short of providing one. From the caption and text, applied to the figure, I gather that by choosing either to run or to raise one's arms, one can control whether it is daytime or nighttime. This is clearly wrong but it is what I am led to think by the paper.

Response 2: Thank you for your suggestion, which we had not considered before. In this figure, we aim to illustrate that "the agent receives observations and optimizes his cognitive model by minimizing variational free energy → the agent makes the optimal action by minimizing expected free energy → the action changes the environment → the environment generates new observations for the agent." We have now modified the image to be simpler to prevent any possible confusion for readers. Correspondingly, we removed the figure of a person raising their hand and the shadowed house in Figure a.

Author response image 9.

Recommendation 3:

I recommend an overhaul in the labelling and methodological explanations for consistency and full reporting. For example, line 73 says sensory input is 's' and the cognitive model is 'q(s),' and the cause of the sensory input is 'p(s|o)' but on the very next line, the cognitive model is 'p(s|o)' and the causes of sensory input are 'q(s).' How this sensory input s relates to 'observations' or 'o' is unclear, and meanwhile, capital S is the set of environmental states. P seems to refer to the generative distribution, but it also means probability.

Response 3: Thank you for your advice. Now we have revised the corresponding labeling and methodological explanations in our work to make them consistent. However, we are not sure how to make a good modification to P here. In many works, P can refer to a certain probability distribution or some specific probabilities.

Recommendation 4:

Even the conception of a "policy" is unclear (Figure 2B). They list 4 possible policies, which are simply the 4 possible sequences of steps, stay-safe, cue-risky, etc, but with no contingencies in them. Surely a complete policy that lists 'cue' as the first step would entail a specification of how they would choose the safe or risky option BASED on the information in that cue

Response 4: Thank you for your suggestion. In active inference, a policy actually corresponds to a sequence of actions. The policy of "first choosing 'Cue' and then making the next decision based on specific information" differs from the meaning of policy in active inference.

Recommendation 5:

I assume that the heavy high pass filtering of the EEG (1 Hz) is to avoid having to baseline-correct the epochs (of which there is no mention), but the authors should directly acknowledge that this eradicates any component of decision formation that may evolve in any way gradually within or across the stages of the trial. To take an extreme example, as Figure 3E shows, the expected rewards for the risky path evolve slowly over the course of 60 trials. The filter would eliminate this.

Response 5: Thank you for your suggestion. The heavy high pass filtering of the EEG (1 Hz) is to minimize the noise in the EEG data as much as possible.

Recommendation 6:

There is no mention of the regression itself in the Methods section - the section is incomplete.

Response 6: Thank you for your suggestion. We have now added the relevant content in the Results section (EEG results at source level, line 337-340):

“The linear regression was run by the "mne.stats.linear regression" function in the MNE package (Activity ∼ Regressor + Intercept, Activity is the activity amplitude of the EEG signal in the source space and regressor is one of the regressors that we mentioned).”

Recommendation 7:

On Lines 260-270 the same results are given twice.

Response 7: Thank you for your suggestion. We have now deleted redundant content.

Recommendation 8:

Frequency bands are displayed in Figure 5 but there is no mention of those in the Methods. In Figure 5b Theta in the 2nd half is compared to Delta in the 1st half- is this an error?

Response 8: Thank you for your suggestion. It indeed was an error (they should all be Theta) and now we have corrected it.

Author response image 10.

Author response:

Reviewer #1 (Public Review):

Summary:

This work sets out to elucidate mechanistic intricacies in inflammatory responses in pneumonia in the context of the aging process (Terc deficiency - telomerase functionality).

Strengths:

Very interesting, conceptually speaking, approach that is by all means worth pursuing. An overall proper approach to the posited aim.

We want to thank the reviewer for taking the time to review our manuscript and for providing positive feedback regarding our research question.

Weaknesses:

The work is heavily underpowered and may have statistical deficits. This precludes it in its current state from drawing unequivocal conclusions.

Thank you for this essential and valuable comment. We fully accept that the small sample size of the Tercko/ko mice is a major limitation of our study and transparently discuss this in our manuscript.

However, due to Animal Welfare regulations, only a reduced number of mice were approved because of the strong burden of disease. Consequently, only three non-infected and five infected mice were available to us. This reduced number of mice presents a clear limitation to our study. However, due to ethical considerations related to animal welfare and sustainability, as well as compliance with German animal welfare regulations, it is not possible to obtain additional Tercko/ko mice to increase the dataset. The animal studies are an important aspect of our study; however, our hypothesis was also investigated at multiple levels, including in an in vitro co-culture model (Figure 5), to ensure comprehensive analysis.

Thus, we clearly demonstrated that S. aureus pneumonia in Tercko/ko mice leads to a more severe phenotype, orchestrated by the dysregulation of both innate and adaptive immune response.

Reviewer #2 (Public Review):

Summary:

The authors demonstrate heightened susceptibility of Terc-KO mice to S. aureus-induced pneumonia, perform gene expression analysis from the infected lungs, find an elevated inflammatory (NLRP3) signature in some Terc-KO but not control mice, and some reduction in T cell signatures. Based on that, They conclude that disregulated inflammation and T-cell dysfunction play a major role in these phenomena.

Strengths:

The strengths of the work include a problem not previously addressed (the role of the Terc component of the telomerase complex) in certain aspects of resistance to bacterial infection and innate (and maybe adaptive) immune function.

We would like to thank the reviewer for the positive feedback regarding our aim to investigate the impact of Terc deletion on the pulmonary immune response to S. aureus.

Weaknesses:

The weaknesses outweigh the strengths, dominantly because conclusions are plagued by flaws in experimental design, by lack of rigorous controls, and by incomplete and inadequate approaches to testing immune function. These weaknesses are as follows

(1)  Terc-KO mice are a genomic knockout model, and therefore the authors need to carefully consider the impact of this KO on a wide range of tissues. This, however, is not the case. There are no attempts to perform cell transfers or use irradiation chimera or crosses that would be informative.

We thank the reviewer for bringing up this important point. The aim of our study, however; was to investigate the impact of Terc deletion in the lung and on the response to bacterial pneumonia, rather than to provide a comprehensive characterization of the Tercko/ko model itself. This characterization of different tissues and cell types has already been conducted by previous studies. For instance, studies that characterize the general phenotype of the model (Herrera et al., 1999; Lee et al., 1998; Rudolph et al., 1999) but also investigations that shed light on the impact of Terc deletion on specific cell types such as microglia (Khan et al., 2015) or T cells (Matthe et al., 2022). The impact of Terc deletion on T cells is also discussed in our manuscript in lines 89 to 105. Furthermore, a section about the general phenotype of the Terc deletion model is included in the introduction in lines 126 to 138. Thus we discussed the relevant literature regarding Tercko/ko mice in our manuscript and attempted to provide a more in-depth characterization of the lung by investigating the inflammatory response to infection as well as changes in the gene expression (Figure 2-4).

(2)  Throughout the manuscript the authors invoke the role of telomere shortening in aging, and according to them, their Terc-KO mice should be one potential model for aging. Yet the authors consistently describe major differences between young Terc-KO and naturally aging old mice, with no discussion of the implications. This further confuses the biological significance of this work as presented.

Thank you for mentioning this relevant point. We want to apologize for the confusion regarding this matter. While Tercko/ko mice are a well-established model for premature aging, these effects become more apparent with increasing generations (G) and thus, G5 and 6 mice are the most affected by Terc deletion (Lee et al., 1998; Wong et al., 2008).

Thus, while Tercko/ko mice are a common model for premature aging, this accelerated aging phenotype is predominantly apparent in later-generation Tercko/ko (G5 and 6) or aged Tercko/ko mice (Lee et al., 1998; Wong et al., 2008). Since the aim of this study was to analyze the impact of Terc deletion on the lung and its immune response to bacterial infections instead of the impact of telomere shortening and telomerase dysfunction, young G3 Tercko/ko mice (8 weeks) were used in this study. This is also mentioned in the lines 131-134. In this study, Tercko/ko mice were used not as a model of aging, but rather as a model specifically for Terc deletion. The old WT mice function as a control cohort to observe possible common but also deviating effects between aging and Terc deletion. In our sequencing data, we observe that uninfected young WT mice are very similar to uninfected Tercko/ko mice. Other studies have also reported this lack of major differences between uninfected WT and Tercko/ko mice in the G3 knockout mice (Kang et al., 2018). Conversely, uninfected young WT and Tercko/ko mice exhibited great differences, for instance, regarding the numbers of differentially expressed genes (Supplemental Figure 1H). Thus, differences between naturally aged mice and young G3 Tercko/ko mice are not surprising. To clarify this aspect we reconstructed the paragraph discussing the Tercko/ko mice (lines 126-134). Additionally we added a paragraph explaining the purpose of the naturally aged mice to the lines 134 to 138:

“As control cohort age-matched young WT mice were utilized. To investigate whether Terc deletion, beyond critical telomere shortening, impacts the pulmonary immune response, we used young Tercko/ko mice. Additionally, naturally aged mice (2 years old) were infected to explore the potential link to a fully developed aging phenotype.”

(3)  Related to #2, group design for comparisons lacks a clear rationale. The authors stipulate that Terc- KO will mimic natural aging, but in fact, the only significant differences seen between groups in susceptibility to S. aureus are, contrary to the authors' expectation, between young Terc-KO and naturally old mice (Figures 1A and B, no difference between young Terc-KO and young wt); or there are no significant differences at all between groups (Figures 1, C, D,).

We thank the reviewer for this essential comment. As mentioned above the Tercko/ko mice in this study are not selected to model natural aging. To model telomerase dysfunction and accelerated aging selection of later generation or aged Tercko/ko mice would have been more suitable.

The lack of statistical significance in some figures is likely due to the heterogeneity of disease phenotype of S. aureus infection in mice, which is a limitation of our study that we discuss in our discussion section in lines 577-583. The phenotype of S. aureus infection can vary greatly within a mouse population, highlighting the limitations of mice as a model for S. aureus infections. To account for this heterogeneity we divided the infected Tercko/ko mice cohort into different degrees of severity based on the clinical score and the presence of bacteria in organs other than the lung (mice with systemic infection).

Despite the heterogeneity especially within the Tercko/ko mice cohort the differences between the knockout and young as well as old WT mice were striking. Including the fatal infections, 80% of the Tercko/ko mice had a severe course of disease, while none of the WT mice displayed a severe course (Figure 1A, B and Supplemental Figure 1A, B). This hints towards a clear role of Terc in the response to S. aureus infection in mice. Thus while in some figures the differences are not significant, strong trends towards a more severe phenotype of S. aureus infection in the Tercko/ko mice regarding bacterial load, score and inflammatory response could be observed in our study.

Another example of inadequate group design is when the authors begin dividing their Terc-KO groups by clinical score into animals with or without "systemic infection" (the condition where a bacterium spreads uncontrollably across the many organs and via blood, which should be properly called sepsis), and then compare this sepsis group to other groups (Supplementary Figures 1G; Figure 2; lines 374-376 and 389- 391). This gives them significant differences in several figures, but because they did not clearly indicate where they applied this stratification in the figure legends, the data are somewhat confusing. Most importantly, methodologically it is highly inappropriate to compare one mouse with sepsis to another one without. If Terc-KO mice with sepsis are a comparator group, then their controls have to be wild-type mice with sepsis, who are dealing with the same high bacterial load across the body and are presumably forced to deploy the same set of immune defenses.

We sincerely appreciate the significant time and effort you have invested in reviewing our manuscript. However, with all due respect, we must point out that the definition of sepsis you have referenced is considered outdated. According to the Third International Consensus Definitions for Sepsis and Septic Shock (Sepsis-3), sepsis is defined as "a life-threatening organ dysfunction caused by a dysregulated host response to infection" (Marvin Singer, 2016, JAMA). Given this fundamental misunderstanding of our findings, we find the comment regarding the inadequacy of our groups to be both dismissive and lacking in scientific merit. We would like to emphasize that the group size used in our study is consistent with accepted standards in infection research. We strongly reject any insinuations of inadequacy that have been repeatedly mentioned throughout the review.

In order to provide a nuanced investigation of disease severity in Tercko/ko mice, we added the term “systemic infection” to the figures whenever the mice were divided into groups of mice with and without systemic infection. This is the case for Figure 2A and Supplemental Figure 1C-E. The division into mice with and without systemic infection is also mentioned in the figure legend of Figure 2A in lines 933 to 936 and for Supplemental Figure 1 in lines 1053-1054. We agree that Supplemental Figure 1G is somewhat confusing as the mice with systemic infection are highlighted in this graph but not included as a separate group within our sequencing analysis. We added a sentence to the figure legend clarifying this (lines 1042-1045):

“Nevertheless, the infected Tercko/ko mice were considered one group for the expression analysis and not split into separate groups for the subsequent analysis.”

Additionally, we revised the section regarding this grouping in different degrees of severity in our Material and Methods section to clarify that this division was only performed for specific analysis (line 191):

“…for the indicated analysis.”

Furthermore, the mice which were classified as systemically infected mice were not septic mice, as mentioned above. Those mice were classified by us as systemically infected based on their clinical score and the presence of bacteria in other organs than the lung as stated in the lines 188-191 and 377-382.

Bacteremia is a symptom of very severe cases of hospital-acquired pneumonia with a very high mortality (De la Calle et al., 2016).

Therefore, the systemically infected mice or rather mice with bacteremia display an especially severe pneumonia phenotype, which is distinct from sepsis. The presence of this symptom in our Tercko/ko mice further highlights the clinical relevance of our study. This aspect was added to the manuscript in the lines 569-571.

“The detection of bacteria in extra pulmonary organs is of particular interest, as bacteremia is a symptom of severe pneumonia and is associated with high mortality (De la Calle et al., 2016).”

(4)  The authors conclude that disregulated inflammation and T-cell dysfunction play a major role in S. aureus susceptibility. This may or may not be an important observation, because many KO mice are abnormal for a variety of reasons, and until such reasons are mechanistically dissected, the physiological importance of the observation will remain unclear.

Two points are important here. First, there is no natural counterpart to a Terc-KO, which is a complete loss of a key non-enzymatic component of the telomerase complex starting in utero.

Second, the authors truly did not examine the key basic features of their model, including the features of basic and induced inflammatory and immune responses. This analysis could be done either using model antigens in adjuvants, defined innate immune stimuli (e.g. TLR, RLR, or NLR agonists), or microbial challenge. The only data provided along these lines are the baseline frequencies of total T cells in the spleen of the three groups of mice examined (not statistically significant, Figure 4B). We do not know if the composition of naïve to memory T cell subsets may have been different, and more importantly, we have no data to evaluate whether recruitment of the immune response (including T cells) to the lung upon microbial challenge is similar or different. So, what are the numbers and percentages of T cells and alveolar macrophages in the lung following S. aureus challenge and are they even comparable or are there issues in mobilizing the T cell response to the site of infection? If, for example, Terc-KO mice do not mobilize enough T cells to the lung during infection, that would explain the paucity in many T-cell- associated genes in their transcriptomic set that the authors report. That in turn may not mean dysfunction of T cells but potentially a whole different set of defects in coordinating the response in Terc-KO mice.

We thank the reviewer for highlighting these important aspects. Regarding the first point, indeed there is no naturally occurring deletion of Terc in humans. However, studies reported reduced expression of Terc and Tert in the tissues of aged mice and rats (Tarry-Adkins et al., 2021; Zhang et al., 2018). Terc itself has been found to have several important immunomodulatory functions such as the activation of the NF- κB or PI3-kinase pathway (Liu et al., 2019; Wu et al., 2022). As those aforementioned pathways are relevant for the immune response to S. aureus infections, the authors were interested in exploring the impact of Terc deletion on the pulmonary immune response. The potential immunomodulatory functions of Terc are discussed in lines 106-121. To further clarify our rationale we added a sentence to the introduction in lines 121-125.

“Interestingly, downregulation of Terc and Tert expression in tissues of aged mice and rats has been found (Tarry-Adkins, Aiken, Dearden, Fernandez-Twinn, & Ozanne, 2021; Zhang et al., 2018).

Therefore, as a potential immunomodulatory factor reduced Terc expression could be connected to age- related pathologies.”

Regarding the second point, as we focused on the effect of Terc deletion in the lung and its role in S. aureus infection, we investigated inflammatory and immune response parameters relevant to this setting. For instance, inflammation parameters in the lungs of all three mice cohorts were measured to investigate differences in the inflammatory response in the non-infected and infected mice (Figure 2A). Those measurements showed no baseline difference in key inflammatory parameters between young WT and Tercko/ko mice, which is consistent with previous findings (Kang et al., 2018). The inflammatory response to infection with S. aureus in the Tercko/ko mice cohort differed significantly from the other cohorts (Figure 2A), hinting towards a dysregulated inflammatory response due to Terc deletion. Furthermore, we investigated general immune cell frequencies such as dendritic cells, macrophages, and B cells in the spleen of all three mice cohorts to gather a baseline understanding of the general immune cell populations. In our manuscript only total T cell frequencies were included due to its relevance for our data regarding T cells (Figure 4B). This data could show that there was no difference of total amount of T cells in the spleen of all three mice cohorts. For a more detailed insight into our analysis we added the frequencies of the other immune cell populations analyzed in the spleen as a Supplemental Figure 3B-F. Additionally, a figure legend for the graphs was added.

Therefore, while we did not analyze baseline frequencies of specific populations of T cells, we analyzed and characterized the inflammatory and immune response of our model in a way relevant to our research question.

The differences observed in T cell marker and TCR gene expression was also partly present between the uninfected and infected Tercko/ko mice such as the complete absence of CD247 expression in infected Tercko/ko, which is however expressed in uninfected mice of this cohort (Figure 4A, C and D). Thus, this effect cannot be solely attributed to an inadequate mobilization of T cells to the lung after infectious challenge. However, we agree that a more detailed insight into recruited immune cells to the lung or frequencies of different T cell populations could contribute to a better understanding of the proposed mechanism and would be an interesting experiment to conduct in further studies. We accept this as a limitation of our study and included it in our discussion section in lines 720-724:

“As total CD4+ T cells were analyzed in this study, it would be useful to investigate specific T cell populations such as memory and effector T cells to elucidate the potential mechanism leading to T cell dysfunctionality in further detail. Additionally, analysis of differences in immune cell recruitment to the lungs between young WT and Tercko/ko mice would be relevant.”

(5)  Related to that, immunological analysis is also inadequate. First, the authors pull signatures from the total lung tissue, which is both imprecise and potentially skewed by differences, not in gene expression but in types of cells present and/or their abundance, a feature known to be affected by aging and perhaps by Terc deficiency during infection. Second, to draw any conclusions about immune responses, the authors would have to track antigen-specific T cells, which is possible for a wide range of microbial pathogens using peptide-MHC multimers. This would allow highly precise analysis of phenomena the authors are trying to conclude about. Moreover, it would allow them to confirm their gene expression data in populations of physiological interest

We thank the reviewer for highlighting this important and relevant point. In our study, we aimed to investigate the role of Terc expression in modulating inflammation and the immune response to S. aureus infection in the lung. To address this, we examined the overall impact of age, genotype, and infection on lung inflammation and gene expression. Therefore, sequencing of total lung tissue was essential for addressing the research question posed. Our findings demonstrate that Tercko/ko mice exhibit a more severe phenotype following S. aureus infection, characterized by an increased bacterial load and heightened lung inflammation (Figures 1 and 2). Furthermore, our data suggest that Terc plays a role in regulating inflammation through activation of the NLRP3 inflammasome, along with the dysregulation of several T cell marker genes (Figures 2, 4, and 5). However, this study lacks a detailed analysis of distinct T cell populations, including antigen-specific T cells, as noted earlier. Investigating these aspects in future studies would be valuable to validate and expand upon our findings. We have incorporated these suggestions into the discussion section (lines 720-724)

“As total CD4+ T cells were analyzed in this study, it would be useful to investigate specific T cell populations such as memory and effector T cells to elucidate the potential mechanism leading to T cell dysfunctionality in further detail. Additionally, analysis of differences in immune cell recruitment to the lungs between young WT and Tercko/ko mice would be relevant.”

Nevertheless, our study provides first evidence of a potential connection between T cell functionality and Terc expression.

Third, the authors co-incubate AM and T cells with S. aureus. There is no information here about the phenotype of T cells used. Were they naïve, and how many S. aureus-specific T cells did they contain? Or were they a mix of different cell types, which we know will change with aging (fewer naïve and many more memory cells of different flavors), and maybe even with a Terc-KO? Naïve T cells do not interact with AM; only effector and memory cells would be able to do so, once they have been primed by contact with dendritic cells bringing antigen into the lymphoid tissues, so it is unclear what the authors are modeling here. Mature primed effector T cells would go to the lung and would interact with AM, but it is almost certain that the authors did not generate these cells for their experiment (or at least nothing like that was described in the methods or the text).

Thank you for bringing up this important question. For the co-cultivation experiment of T cells and alveolar macrophages, total CD4+ T cells of both young WT and Tercko/ko were used. We did not select for a specific population of T cells. Our sequencing data indicated the complete downregulation of CD247 expression, which is an important part of the T cell receptor, in the lungs of infected Tercko/ko mice (Figure 4A, C and D). Given that this factor is downregulated under chronic inflammatory conditions, we investigated the impact of the inflammatory response in alveolar macrophages on the expression of various T cell-derived cytokines, as well as CD247 expression (Figure 5D, E) (Dexiu et al., 2022). This aspect is also highlighted in the discussion in lines 623-637. Therefore, a co-cultivation model of T cells and alveolar macrophages was established and confronted with heat-killed S. aureus to elicit an inflammatory response of the macrophages. To emphasize this purpose, we have revised our statement about the model setup in lines 517-519 of the manuscript:

“An overactive inflammatory response could be a potential explanation for the dysregulated TCR signaling.”

The authors hope this will clarify the intent behind the model setup.

(6)  Overall, the authors began to address the role of Terc in bacterial susceptibility, but to what extent that specifically involves inflammation and macrophages, T cell immunity, or aging remains unclear at present.

We thank the reviewer for the helpful and relevant comments. The authors accept the limitations of the presented study such as the reduced number of Tercko/ko mice and the limitations of murine models for S. aureus infection itself and discuss those in the discussion section in the lines 559-561; 577-583; 690-692 and 720-726. However, we hope that our responses have provided sufficient evidence to convince the reviewer that our data supports a clear role for Terc expression in regulating the immune response to bacterial infections, particularly with respect to inflammation and its potential connection to T cell functionality.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:<br /> I really enjoyed this manuscript from Torsekar et al on "Contrasting responses to aridity by

different-sized decomposers cause similar decomposition rates across a precipitation gradient". The authors aimed to examine how climate interacts with decomposers of different size categories to influence litter decomposition. They proposed a new hypothesis: "The opposing climatic dependencies of macrofauna and that of microorganisms and mesofauna should lead to similar overall decomposition rates across precipitation gradients".

This study emphasizes the importance as well as the contribution of different groups of organisms (micro, meso, macro, and whole community) across different seasons (summer with the following characteristics: hot with no precipitation, and winter with the following characteristics: cooler and wetter winter) along a precipitation gradient. The authors made use of 1050 litter baskets with different mesh sizes to capture decomposers contribution. They proposed a new hypothesis that was aiming to understand the "dryland decomposition conundrum". They combined their decomposition experiment with the sampling of decomposers by using pittfall traps across both experiment seasons. This study was carried out in Israel and based on a single litter species that is native to all seven sites. The authors found that microorganism contribution dominated in winter while macrofauna decomposition dominated the overall decomposition in summer. These seasonality differences combined with the differences in different decomposers groups fluctuation along precipitation resulted in similar overall decomposition rates across sites.<br /> I believe this manuscript has a potential to advance our knowledge on litter decomposition.

Strengths:

Well design study with combination of different approaches (methods) and consideration of seasonality to generalize pattern.

The study expands to current understanding of litter decomposition and interaction between factors affecting the process (here climate and decomposers).

Weaknesses:

The study was only based on a single litter species.

We now discuss the advantages and limitations of this approach in the methods and devote a completely new paragraph to this important point in the discussion (lines 394-401).

Reviewer #2 (Public Review):

Summary: Torsekar et al. use a leaf litter decomposition experiment across seasons, and in an aridity gradient, to provide a careful test of the role of different-sized soil invertebrates in shaping the rates of leaf litter decomposition. The authors found that large-sized invertebrates are more active in the summer and small-sized invertebrates in the winter. The summed effects of all invets then translated into similar levels of decomposition across seasons. The system breaks down in hyper-arid sites.

Strengths: This is a well-written manuscript that provides a complete statistical analysis of a nice dataset. The authors provide a complete discussion of their results in the current literature.

Weaknesses:

I have only three minor comments. Please standardize the color across ALL figures (use the same color always for the same thing, and be friendly to color-blind people).

Thank you for this important suggestion. We have now changed all figures to standardize all colors and chose a more color-blind friendly pallete.

Fig 1 may benefit from separating the orange line (micro and meso) into two lines that reflect your experimental setup and results. I would mention the dryland decomposition conundrum earlier in the Introduction.

We based our novel hypotheses on a thorough literature search. Accordingly, decomposition is expected to be positively associated with moisture, regardless of the decomposer body size. Our contribution to theory was to suggest that macro-detritivores may respond very differently to climatic conditions and dominate litter decomposition in warm arid-lands (we listed the reasons in the text). Consequently, we did not distinguish between microorganisms and mesofauna. We assumed that both groups inhabit the litter substrate and have limited adaptation to dry conditions. Our results provide strong evidence that this presumption is likely wrong and that mesofauna respond to climate very differently from micro-decomposers. Yet, we cannot use hindsight understanding to improve our original hypothesis. We now emphasize this important point at the discussion as important future direction. 

Although we are very appreciative and pleased with the reviewer enthusiasm to highlight the importance of our work as a possible solution to the longstanding dryland decomposition conundrum, we decided not to move it to the introduction. This is because we think that our work is not centred on resolving the DDC but provides more general principles that may lead to a paradigm shift in the way ecologists study nutrient cycling across ecosystems.

And the manuscript is full of minor grammatical errors. Some careful reading and fixing of all these minor mistakes here and there would be needed.

We apologize and did our best to find and fix those mistakes

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I really enjoyed this manuscript from Torsekar et al on "Contrasting responses to aridity by different-sized decomposers cause similar decomposition rates across a precipitation gradient". The authors aimed to examine how climate interacts with decomposers of different size categories to influence litter decomposition. They proposed a new hypothesis: "The opposing climatic dependencies of macrofauna and that of microorganisms and mesofauna should lead to similar overall decomposition rates across precipitation gradients".

This study emphasizes the importance as well as the contribution of different groups of organisms (micro, meso, macro, and whole community) across different seasons (summer with the following characteristics: hot with no precipitation, and winter with the following characteristics: cooler and wetter winter) along a precipitation gradient. The authors made use of 1050 litter baskets with different mesh sizes to capture decomposers contribution. They proposed a new hypothesis that was aiming to understand the "dryland decomposition conundrum". They combined their decomposition experiment with the sampling of decomposers by using pitfall traps across both experiment seasons. This study was carried out in Israel and based on a single litter species that is native to all seven sites. The authors found that microorganism contribution dominated in winter while macrofauna decomposition dominated the overall decomposition in summer. These seasonality differences combined with the differences in different decomposers groups fluctuation along precipitation resulted in similar overall decomposition rates across sites.

I believe this manuscript has the potential to advance our knowledge on litter decomposition. Below i provide my general and specific comments.

General comments:

(1) Study in general is well designed and well thought beforehand,

(2) Study aims to expand the current understanding of the dryland decomposition conundrum

(3) The should put a caveat to the fact they only use one litter species and call for examining litter mixture in the same gradient.

(4) Please check the way you reduce the random effects from your initial model, I have provided a better way to do so in my specific comments

(5) For Figure 1, authors can check my comment on this and see if they could revise the figure.

Thank you for the positive feedback and your valuable comments. We have tried to best address all comments and suggestions for improvement and clarification

Specific comments

Line # 57 Please write "Theory suggests" instead of "Theory suggest"

We changed the text as suggested

Line # 70, please write "Indeed, handful evidence shows" instead of "Indeed, handful evidence show"

We changed the text as suggested

Figure 1: I like this conceptual framework. I have a silly question, why is it that the slopes of the whole community at the beginning (between Hyperarid and Arid) is the same as the Macro fauna, I would think the slope should be higher as this is adding up right? and also the same goes for the decomposition of whole community later on. For me this should reflect the adding or summing up (if i am right) then the authors should think about how this could be reflected in the figure.

We agree with your interpretation that the whole community decomposition reflects the addition by constituent decomposers. The slope of the whole community decomposition between hyper-arid and arid is slightly higher than the one of macro decomposition to reflect the additive effect of macro with meso+micro decomposition. We have now changed the figure slightly to make this point more visible (Line 106).

Line # 111 Please make "Methods" bold as well to be consistent with others headings.

We changed the formatting as suggested

Line #125 and in other lines as well please replace "X" by "x" to denote multiplication.

We changed the formatting as suggested

Table 1 Please add "*" to climate like this "Climate*" so that the end note of the table could make sense

Thank you for this suggestion. We have now added the asterisk referring to the note below the Table.

Figure 2, please consider putting at line #133, mean annual precipitation (MAP), as such for line # 135 You can directly says The precipitation map ....

We made both changes as suggested.

Line # 138 I would not use the different units for the same values. I do understand that you want to emphasize the accuracy but i would write instead 3 +- 0.001 g

We changed the units as suggested.

Line # 145, how is the litter basket customized to rest at 1 cm above ground level?

We have now clarified –that we cut-open windows one centimeter above the cage floor. The cages were positioned on the soil (line 144).

Lines # 181-183, I like the approach of checking the necessity of having the random effects. However, it has been reported that likelihood ratio test (LRT) are not really reliable to test for random effects. I will suggest you rather use permutations instead. I think the function is confint(MODEL) you need to specify the number of permutation the higher the better but you should start with 99 first and see how the results look like if promising then you can even go to 9999. But it will need computation power and and time.

Thank you for the suggestion. We now used a simulation-based exact test, instead of a LRT, to examine the random effect, as recommended by the authors from the “lme4” package. As recommended, we used 9999 simulations. The simulation test yielded a similar result to those originally reported (see lines 181-183).

Line # 187, 188, 188, please do not use capital letter to start mesofauna, macrofauna and whole-community

We changed the formatting as suggested

Line # 205 Please add the version number of R in the text.

We now included the version number as suggested.

Line # 209-211, could you please check whether "then" is the word you want to use or "than"

Our bad- we indeed meant “than” and have made the appropriate changes.

Line # 227 and in other places as well please provide the second degree of freedom of the F test.

Thank you for this important comment. We have now added the second degree of freedom to the relevant results (lines 229, 232).

Figure 3 and Figure 4 show some results that are negative, can you please explain what might be the reasons behind this?

We now explain this important point in the figures’ captions.

Figure 5 Please add label to the x-axis.

Thank you-we have now included a label.

Line # 357, the sentence "... meso-decomposition, like microbial decomposition,...", I don't understand which criteria authors used to classify microbial decomposition as "meso-decomposition"?

We now remove this potential cause of confusion by using the term ‘meso-decomposition’ to distinguish from microbial decomposition (Line 366).

Line # 380 Kindly put "per se" in italic.

We changed the formatting as suggested

References

The references format are not consistent. For example for the same journal (say Trends in Ecology and Evolution) the authors sometimes wrote the full name like at line # 36 (and also realize that "vol" should not be written as such) but wrote the abbreviations at line #42

Our bad- we apologize and carefully checked all references to make sure the style is consistent.

Author response:

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

(1) Combined Public Reviews:

Strengths:

This work investigates the role of DNAH3 in sperm mobility and male infertility and utilised gold-standard molecular biology techniques, showing strong evidence of its role in male infertility. All aspects of the study design and methods are well described and appropriate to address the main question of the manuscript. The conclusions drawn are consistent with the analyses conducted and supported by the data.

We extend our sincere gratitude to the expert reviewers for their valuable comments and insightful suggestions.

Weaknesses:

(1.1) The manuscript lacks a comparison with previous studies on DNAH3 in the Discussion section.

We thank the reviewers' comments.

Recently, Meng et al. identified bi-allelic variants in DNAH3 from patients diagnosed with asthenoteratozoospermia, revealing multiple morphological defects and a disrupted "9+2" arrangement in the patients' sperm (https://doi.org/10.1093/hropen/hoae003, PMID: 38312775). Furthermore, they generated Dnah3 KO mice, which were infertile, and exhibited moderate morphological abnormalities with a normally structured “9 + 2” microtubule arrangement. In our study, we also observed similar phenotypic differences between the phenotypes of DNAH3-deficient patients and Dnah3 KO mice. These findings indicate that DNAH3 may play crucial yet distinct roles in human and mouse male reproduction. Additionally, our TEM analysis demonstrated a notable absence of IDAs in sperm from both DNAH3-deficent patients and Dnah3 KO mice, resembling the findings of Meng et al. To further investigate, we conducted immunofluorescent staining and western blotting to assess the levels of IDA-associated proteins (DNAH1, DNAH6 and DNALI1) and ODA-associated proteins (DNAH8, DNAH17 and DNAI1) in sperm samples from both our DNAH3-deficient patients and Dnah3 KO mice. Our data revealed a reduction in IDA-associated protein levels and comparable ODA-associated protein levels in comparison to normal controls and WT mice, respectively, thus corroborating the TEM observations. These results suggest that DNAH3 is involved in sperm flagellar development in human and mice, specifically through its role in the assembly of IDAs.

Intriguingly, in our study, none of the patients with DNAH3 deficiency reported experiencing any of the principal symptoms associated with PCD. Additionally, our Dnah3 KO mice exhibited normal ciliary development in the lung, brain, eye, and oviduct. Similarly, Meng et al. did not mention any PCD symptoms in their DNAH3-deficient patients, and their Dnah3 KO mice also demonstrated normal ciliary morphology in the trachea and brain. These combined observations suggest that DNAH3 may play a more significant role in sperm flagellar development than in other motile cilia functions. Given that DNAH3 is expressed in ciliary tissues, its role in these tissues remains intriguing and could be elucidated through sequencing of larger cohorts of individuals with PCD.

We have added these discussions in line 267 to 283, and line 300 to 303.

(1.2) The variants of DNAH3 in four infertile men were identified through whole-exome sequencing. Providing an overview of the WES data would be beneficial to offer additional insights into whether other variants may contribute the infertility. This could also help explain why ICSI only works for two out of four patients with DNAH3 variants.

We thank the reviewer's helpful suggestions.

We have deposited the raw whole-exome sequencing data in the National Genomics Data Center (NGDC) (https://ngdc.cncb.ac.cn/, accession number: HRA007467). The clean reads, sequencing depth, sequencing coverage, and mapping quality of the WES on the patients are listed below (Table R1). A summary of WES has been presented in Table S1.

Author response table 1.

Quality of whole exome sequencing on infertile men.

The variants identified through WES were annotated and filtered using Exomiser. Next, the variants were screened to obtain candidate variants based on the following criteria: (1) the allele frequency in the East Asian population was less than 1% in any database, including the ExAC Browser, gnomAD, and the 1000 Genomes Project; (2) the variants affected coding exons or canonical splice sites; (3) the variants were predicted to be possibly pathogenic or damaging.

Following filtering and screening, the numbers of candidate variants obtained were as follows: Patient 1: 98, Patient 2: 101, Patient 3: 67, and Patient 4: 91(Table S1). Subsequently, we utilized the Human Protein Atlas (HPA) database (https://www.proteinatlas.org/) and Mouse Genome Informatics (MGI) database (https://informatics.jax.org/) to analyze the expression patterns of corresponding genes. Variants whose corresponding genes were not expressed in the human or mouse testis were excluded from further consideration. We also consulted OMIM database and reviewed relevant literature to exclude variants associated with diseases unrelated to male infertility. Additionally, considering the assumption of a recessive inheritance pattern, we excluded all monoallelic variants. Ultimately, only bi-allelic variants in DNAH3 (NG_052617.1, NM_017539.2, NP_060009.1) remained, suggesting as the pathogenic variants responsible for the infertility of the patients (Table S1). These DNAH3 variants were verified by Sanger sequencing on DNA from the patients' families.

We have added the overview of the WES in Table S1 and supplemented the analysis process of WES data in line 100 to 106, and line 348 to 360.

Additionally, we did not identify any pathogenic variants that associated with fertilization failure and early embryonic development in the two patients with failed ICSI outcomes. Therefore, these different ICSI outcomes might be attributed to additional unexplained factors from the female partners.

(1.3) Quantification of images would help substantiate the conclusions, particularly in Figures 2, 3, 4, and 6. Improved images in Figures 3A, 4B, and 4C, would help increase confidence in the claims made.

In response to reviewer’s valuable suggestions. We presume that the reviewer means quantification of images in Figure S6, but not Figure 6.

We have compiled statistics for results shown in Figures 2, 3, 4, and S6. Specifically:

- The percentages of abnormal flagellar morphology in normal control and patients, associated with the observations in Figure 2A, have been shown in Figure S1A.

- The percentages of aberrant axonemal ultrastructure in different cross-sections of sperm from in normal control and patients, correspond to the findings in Figure 3A, have been presented in Figure S1B.

- The percentages of abnormal flagellar morphology in WT mice and Dnah3 KO mice have been shown in Figure S7A.

- The percentages of aberrant axonemal arrangement in different cross-sections of sperm from WT mice and Dnah3 KO mice, corresponding to the findings in Figure 4B, have been presented in Figure S7C.

- The percentages of microtubule doublets presenting IDAs in sperm from WT mice and Dnah3 KO mice, related to Figure 4B, have been detailed in Figure S7D.

- The percentages of malformed mitochondria in the midpiece of sperm from WT mice and Dnah3 KO mice, associated with the observations in Figure 4C, have been presented in Figure S7E.

Moreover, we have revised Figures 3A, 4B, and 4C by replacing the unclear TEM images.

(2) Reviewer #1 (Recommendations for The Authors):

(2.1) Please add reference(s) that support what is claimed in lines 83-84.

We are very grateful for the reviewer's careful comments, we have added a reference that describing the homology and expression of DNAH3.

(2.2) In line 286, change "suggested" to "suggest".

Thanks for the reviewer's comments. We have corrected the grammar.

(2.3) Please add reference(s) that support what is claimed in lines 359-360.

According to the reviewer’s suggestions, we have included references detailing the STA-PUT velocity sedimentation for isolation of single human and mouse testicular cells.

(2.4) In line 365, change "in" to "into".

Thanks for the reviewer’s careful comments, we have corrected this word.

(2.5) In Figure 7, I suggest changing "patients" to "wife or partners of patient". Given that the results are indeed from the spouses of the infertile men, I suggest making this small change to keep the consistency and clarity of what the authors did.

In response to reviewer’s kind suggestions, we have replaced “Patient” by “partners of Patient” and revised Figure 7.

(3) Reviewer #2 (Recommendations for The Authors):

(3.1) A summary of the WES data would be needed (i.e. number of reads, mapping quality, etc). As mentioned in the public review, it would be beneficial to present a summary of all variants identified in the data and clarify whether DNAH3 is the only gene that contains variants and whether these variants have been validated.

Many thanks for reviewer’s kind suggestions.

The clean reads, sequencing depth, sequencing coverage, and mapping quality of the WES on the patients are listed (see author response table 1) A summary of WES has been presented in Table S1.

The variants identified through WES were annotated and filtered using Exomiser. Next, the variants were screened to obtain candidate variants based on the following criteria: (1) the allele frequency in the East Asian population was less than 1% in any database, including the ExAC Browser, gnomAD, and the 1000 Genomes Project; (2) the variants affected coding exons or canonical splice sites; (3) the variants were predicted to be possibly pathogenic or damaging.

Following filtering and screening, the numbers of candidate variants obtained were as follows: Patient 1: 98, Patient 2: 101, Patient 3: 67, and Patient 4: 91(Table S1). Subsequently, we utilized the Human Protein Atlas (HPA) database (https://www.proteinatlas.org/) and Mouse Genome Informatics (MGI) database (https://informatics.jax.org/) to analyze the expression patterns of corresponding genes. Variants whose corresponding genes were not expressed in the human or mouse testis were excluded from further consideration. We also consulted OMIM database and reviewed relevant literature to exclude variants associated with diseases unrelated to male infertility. Additionally, considering the assumption of a recessive inheritance pattern, we excluded all monoallelic variants. Ultimately, only bi-allelic variants in DNAH3 (NG_052617.1, NM_017539.2, NP_060009.1) remained, suggesting as the pathogenic variants responsible for the infertility of the patients (Table S1). These DNAH3 variants were verified by Sanger sequencing on DNA from the patients' families.

We have added the overview of the WES in Table S1 and supplemented the analysis process of WES data in line 100 to 106, and line 348 to 360.

(3.2) It would be beneficial to the scientific community if the raw data of WES could be uploaded to a public data repository, such as GEO.

According to the reviewer's suggestion, we have deposited the raw whole-exome sequencing data in the National Genomics Data Center (NGDC) (https://ngdc.cncb.ac.cn/, accession number: HRA007467) and described its availability in the "Data Availability" section.

(3.3) In line 115, it is not clear how the prediction was made. Clarifying them by adding citations or describing methods that predict these pathways/functions would help strengthen it.

Thanks for the reviewer's comments.

SIFT, PolyPhen-2, MutationTaster and CADD assess the deleteriousness of genetic variants by considering genomic features and evolutionary constraint of the surrounding sequence or structural and chemical property altercations by the amino acid substitutions. We have added websites and references of these tools in the manuscript (line 116 to 118).

Here are the principles of these tools.

- The SIFT considers the position at which the change occurred and the type of amino acid change, and then to predict whether an amino acid substitution in a protein will affect protein function [https://sift.bii.a-star.edu.sg/, PMID: 12824425].

- The PolyPhen-2 predicts the impact of an amino acid substitution on a human protein by considering several features, including sequence, phylogenetic, and structural information [http://genetics.bwh.harvard.edu/pph2/, PMID: 20354512].

- The MutationTaster utilizes a Bayes classifier to predict the functional consequences of amino acid substitutions, intronic and synonymous changes, short insertions/deletions (indels), etc. [https://www.mutationtaster.org/, PMID: 24681721].

- The CADD scores are based on diverse genomic features derived from surrounding sequence context, gene model annotations, evolutionary constraint, epigenetic measurements, and functional predictions [https://cadd.gs.washington.edu/, PMID: 30371827].

(4) Reviewer #3 (Recommendations for The Authors):

(4.1) Please ensure that all gene names used in your manuscript have been approved by the HUGO nomenclature committee. For example, "c.3590C>T (p.P1197L)" should be described as "c.3590C>T (Pro1197Leu)".

In response to the reviewer's suggestion, we have improved all the names of gene and variants according to the HUGO nomenclature committee and HGVS Variant Nomenclature Committee, respectively.

(4.2) For Table 1, the authors should provide the rates of abnormal sperm morphologies using the sperm cells from normal male controls.

Thanks for the reviewer’s careful comments. Consistent with the WHO laboratory manual (World Health Organization. WHO laboratory manual for the examination and processing of human semen. World Health Organization, 2021.), our routine semen analysis establishes 4% as the minimum rate of sperm with normal morphology but does not define the maximum rate of various tail defects. However, we reviewed the routine semen analysis on the normal controls in our study, and the approximate distribution of sperm with various flagellar in the normal controls was as follows: normal flagella, 78.6%; absent flagella, 1.7%; short flagella, 0.6%; coiled flagella, 12.5%; bent flagella, 7.9%; irregular flagella, 1.8%.

(4.3) In Table 2, "Mutation Tester" or "Mutation Taster"?

We thank the reviewer’s comments. It should be "MutationTaster", and we have corrected this mistake in Table 2 and the manuscript.

(4.4) In Figure 2B, the bars for patient 1 should be aligned. 

Following the reviewer's valuable suggestion, we have ensured consistent scar bar alignment in Figure 2B and implemented this alignment throughout all other figures.

(4.5) In Figure 3A, what about the ultrastructure for sperm heads in DNAH3 deficient sperm cell? The authors previously mentioned abnormalities in sperm head morphologies (Figure 2B) in patients with DNAH3 mutations.

We thank the reviewers for their kind comments. A small fraction of abnormal sperm head of our patients was captured under TEM, manifested by round head with loose chromatin (Author response image 1)

Author response image 1.

Ultrastructure of sperm head from DNAH3-deficient infertile men. TEM analysis revealed a fraction of round head with loose chromatin in patients harboring DNAH3 variants. Scale bars, 200 nm.

(4.6) In Figure S6, the authors should provide the rates of abnormal sperm morphologies for Dnah3 KO male mice.

In response to the reviewer's valuable suggestion, we have quantified morphological defects in spermatozoa from both Dnah3 KO and WT mice. Compared to about 17% morphological abnormalities in sperm from WT mice, the morphological abnormalities in sperm from Dnah3 KO mice were about 37%. The results are presented in the revised Figure S7.

Author response:

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

eLife assessment

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

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

Reviewer #2 (Public Review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

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

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

Reviewer #3 (Public Review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

Lines 399 – 402:

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

Lines 475 – 480:

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

Lines 528 – 532:

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

Lines 543 – 550:

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

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

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

Our changes are detailed below:

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

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

Lines 149 – 155:

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

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

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

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

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

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

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

Supplement, lines 172 – 189:

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

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

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

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

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

Specifically, in terms of parameter orthogonality:

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

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

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

Supplement, lines 175 – 180:

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

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

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

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

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

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

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

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

Lines 149 – 155:

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

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

Lines 698 – 709:

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

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

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

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

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

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

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

Lines 317 – 323:

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

(2) Recommendations for improving the writing and presentation.

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

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

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

Lines 107 – 112:

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

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

Lines 800 – 814:

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

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

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

Lines 356 – 383:

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

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

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

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

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

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

Lines 399 – 402:

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

Lines 475 – 480:

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

Lines 528 – 532:

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

Lines 543 – 550:

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

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

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

Lines 83 – 84:

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

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

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

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

Lines 97 – 98:

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

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

(3) Minor corrections to the text and figures.

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

Reviewer #2 (Recommendations For The Authors):

I did have a few more minor comments:

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

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

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

Lines 161 – 165:

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

In the Methods section, we have added the following.

Lines 617 – 622:

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

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

Lines 195 – 213:

“3.2 Proportion of accepted but failed trials

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

“3.3 Exertion of “extra effort”

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

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

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

Lines 442 – 445:

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

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

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

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

Lines 642 – 655:

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

- The word "metabolic" is misspelled in Table 1

- Figure 2 is missing panel label "C"

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

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

Reviewer #3 (Recommendations For The Authors):

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

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

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

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

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

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

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

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

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

The simulation results are now detailed in the Supplement.

Lines 25 – 46:

“1.2.1 Parameter recoveries including inverse temperature

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

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

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

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

Lines 698 – 709:

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

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

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

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

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

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

Lines 258 – 261:

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

We have added the following paragraph to our discussion.

Lines 491 – 502:

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

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

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

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

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

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

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

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

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

Lines 67 – 68:

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

Lines 248 – 251:

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

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

Lines 755 – 759:

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

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

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

Lines 317 – 320:

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

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

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

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

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

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

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

Lines 101 – 106:

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

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

Lines 185 – 187:

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

Lines 215 – 221:

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

Lines 252 – 258:

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

Lines 258 – 263:

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

Lines 268 – 270:

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

Lines 295 – 298:

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

Lines 344 – 355:

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

Lines 390 – 393:

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

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Strengths: 

Overall the work is novel and moves the field of Alzheimer's disease forward in a significant way. The manuscript reports a novel concept of aberrant activity in VIP interneurons during the early stages of AD thus contributing to dysfunctions of the CA1 microcircuit. This results in the enhancement of the inhibitory tone on the primary cells of CA1. Thus, the disinhibition by VIP interneurons of Principal Cells is dampened. The manuscript was skillfully composed, and the study was of strong scientific rigor featuring well-designed experiments. Necessary controls were present. Both sexes were included.

We express our gratitude to the reviewer for their keen appreciation of our efforts and their enthusiasm for the outcomes of this research.

Limitations:

(1) The authors attributed aberrant circuit activity to the accumulation of "Abeta intracellularly" inside IS-3 cells. That is problematic. 6E10 antibody recognizes amyloid plaques in addition to Amyloid Precursor Protein (APP) as well as the C99 fragment. There are no plaques at the ages 3xTg mice were examined. Thus, the staining shown in Figure 1a is of APP/C99 inside neurons, not abeta accumulations in neurons. At the ages of 3-6 months, 3xTg starts producing abeta oligomers and potentially tau oligomers as well (Takeda et al., 2013 PMID: 23640054; Takeda et al., 2015 PMID: 26458742 and others). Emerging literature suggests that abeta and tau oligomers disrupt circuit function. Thus, a more likely explanation of abeta and tau oligomers disrupting the activity of VIP neurons is plausible.

The Reviewer correctly points out that 3xTg-AD mice typically do not exhibit plaques before 6 months of age, with limited amounts even up to 12 months, particularly in the hippocampus. To the best of our knowledge, the 6E10 antibody binds to an epitope in APP (682-687) that is also present in the Abeta (3-8) peptide. Consequently, 6E10 detects full-length APP, α-APP (soluble alpha-secretase-cleaved APP), and Abeta (LaFerla et al., 2007). Nonetheless, we concur with the Reviewer's observation that the detected signal includes Abeta oligomers and the C99 fragment, which is currently considered an early marker of AD pathology (Takasugi et al., 2023; Tanuma et al., 2023). Studies have demonstrated intracellular accumulation of C99 in 3-month-old 3xTg mice (Lauritzen et al., 2012), and its binding to the Kv7 potassium channel family, which results in inhibiting their activity (Manville and Abbott, 2021). If a similar mechanism operates in IS-3 cells, it could explain the changes in their firing properties observed in our study. Consequently, we have revised the manuscript to include this crucial information in both the Results and Discussion sections.

(2) Authors suggest that their animals do not exhibit loss of synaptic connections and show Figure 3d in support of that suggestion. However, imaging with confocal microscopy of 70micron thick sections would not allow the resolution of pre- and post-synaptic terminals. More sensitive measures such as electron microscopy or array tomography are the appropriate techniques to pursue. It is important for the authors to either remove that data from the manuscript or address the limitations of their technique in the discussion section. There is a possibility of loss of synaptic connections in their mouse model at the ages examined.

We appreciate the Reviewer’s perspective on the techniques used for imaging synaptic connections. While we acknowledge the limitations of confocal microscopy for resolving pre- and post-synaptic structures in thick sections, we respectfully disagree regarding the exclusive suitability of electron microscopy (EM). Our approach involved confocal 3D image acquisition using a 63x objective at 0.2 um lateral resolution and 0.25 Z-step, providing valuable quantitative insights into synaptic bouton density. Despite the challenges posed by thick sections, this method together with automatic analysis allows for careful quantification. Although EM offers unparalleled resolution, it presents challenges in quantification. We have included the important details regarding image acquisition and analysis in the revised manuscript.

Reviewer #2 (Public Review):

Summary:

The submitted manuscript by Michaud and Francavilla et al., is a very interesting study describing early disruptions in the disinhibitory modulation exerted by VIP+ interneurons in CA1, in a triple transgenic model of Alzheimer's disease. They provide a comprehensive analysis at the cellular, synaptic, network, and behavioral level on how these changes correlate and might be related to behavioral impairments during these early stages of the disease.

Main findings:

- 3xTg mice show early Aß accumulation in VIP-positive interneurons.

- 3xTg mice show deficits in a spatially modified version of the novel object recognition test. - 3xTg mice VIP cells present slower action potentials and diminished firing frequency upon current injection.

- 3xTg mice show diminished spontaneous IPSC frequency with slower kinetics in Oriens / Alveus interneurons.

- 3xTg mice show increased O/A interneuron activity during specific behavioral conditions. - 3xTg mice show decreased pyramidal cell activity during specific behavioral conditions.

Strengths:

This study is very important for understanding the pathophysiology of Alzheimer´s disease and the crucial role of interneurons in the hippocampus in healthy and pathological conditions.

We are thankful to the reviewer for their insightful recognition of our efforts and their enthusiasm for the results of this research.

Weaknesses:

Although results nicely suggest that deficits in VIP physiological properties are related to the differences in network activity, there is no demonstration of causality.

We completely agree with the reviewer's observation regarding the lack of demonstration of causality in our results. Investigating causality in the relationship between deficits in VIP physiological properties and differences in network activity is indeed a crucial aspect of this project. However, achieving this goal will require a significant amount of time and dedicated manipulations in a new mouse model (VIP-Cre-3xTg). We appreciate the importance of this line of investigation and consider it as a priority for our future research endeavors.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Limitations:

(1) The authors should describe their model and state the age at which these mice start depositing amyloid plaques and neurofibrillary tangles. Readers might not be familiar with this model. It is also important to mention that circuit disruptions are assessed prior to plaque and tangle formation.

We have included a detailed description of the 3xTg-AD mouse model in the Introduction section, including information on the age at which amyloid plaques and neurofibrillary tangles begin to appear. Additionally, we have clarified that circuit disruptions were assessed before the formation of plaques and tangles. These details have been added to both the Introduction and the Results sections to ensure clarity for readers unfamiliar with the model.

(2) Ns are presented in Supplemental Table 1. Units are presented in a note to Supplementary Table 1. It would be advisable to specify Ns and units as the data is being presented in the results section or figure legends for easy access.

We have now included the Ns (sample sizes), specifying the number of cells or sections and the number of experimental animals, directly within the Results section and in the figure legends. This ensures that readers have immediate access to this information without needing to refer to the supplementary materials.

(3) Several typos require correction:

a. "mamory" - Line 22, page 5.

b. The term "Interneurons" is abbreviated as both "INs" and "IN" throughout the manuscript. The author should consistently choose one abbreviation.

We have corrected the typo "mamory" to "memory" on line 22, page 5. Additionally, we have standardized the abbreviation for "Interneurons" to "INs" throughout the manuscript for consistency.

(4) Note 2 in Supplementary Table 1 states that animals of both sexes with equal distribution were used throughout the study. It would be best for the reader to assess the data distribution based on sex. Thus, it is advisable for the authors to depict male and female data points as distinct symbols throughout the figures.

Unfortunately, we do not have detailed sex-disaggregated data for all datasets, which limits our ability to depict male and female data points separately across all figures. Therefore, we have opted to pool data from both sexes for a more comprehensive analysis. We believe this approach maintains the robustness of our findings.

Reviewer #2 (Recommendations for the authors):

Major Points:

- To keep the logical line of reasoning and to be able to interpret the results, it would be important to use the same metrics when comparing the population activity of O/A interneurons and principal cells in the different behavioral conditions.

We have revised Figures 4 and 5 to enhance the coherence in data presentation. This includes using consistent metrics for comparing the population activity of both O/A interneurons and principal cells across different behavioral conditions. These changes ensure a clearer and more logical interpretation of the results.

- Although results nicely suggest that deficits in VIP physiological properties are related to the differences in network activity, there is no demonstration of causality. Would it be possible to test if manipulating VIP neurons one could obtain such specific results? Alternatively, it could be discussed more in detail how the decrease in disinhibition could lead to the changes in network activity demonstrated here.

We agree with the reviewer that establishing causality between VIP neuron deficits and changes in network activity would be very important. However, demonstrating causality would require a new line of investigation, involving the use of specific mouse models to selectively manipulate VIP neurons. This is an exciting direction that we plan to prioritize in our future research. For this study, we have included a discussion on the potential mechanisms by which decreased disinhibition might lead to the observed changes in network activity. Specifically, we propose that in young adult 3xTg-AD mice, the altered firing of I-S3 cells may lead to enhanced inhibition of principal cells. This could shift the excitation/inhibition balance, input integration and firing output of principal cells thereby impacting overall network activity. These points are discussed in detail in the revised Discussion section.

- On the same lines the correlations showed in the manuscript, would be more robust if there was an in vivo demonstration that 3xTg mice indeed show decreased activity in vivo. The same experiments could also clarify if VIP cells in control animals are more active at the time of decision-making and during object exploration as suggested in the manuscript.

Thank you for your comment. In response to the point raised, we would like to highlight that we have recently documented the increased activity of VIP-INs in the D-zone of the T-maze and during object exploration in a study published in Cell Reports (Tamboli et al., 2024). This publication is now referenced in our manuscript to support our findings. Regarding the in vivo activity of 3xTg mice, our observations indicated no significant differences in major behavioral patterns such as locomotion, rearing, and exploration of the T-maze when comparing Tg and non-Tg mice. These findings are presented in detail in Figure 4c and Supplementary Fig. 5. We believe these data support the robustness of our correlations by demonstrating that the overall behavioral activity of 3xTg mice is comparable to that of non-transgenic controls, thus focusing attention on the specific roles of VIP-INs in early prodromal state of AD pathology.

Minor Points:

- Figure 1c: Heading of VIP-Tg should have capital letters.

Thank you for pointing that out. We have corrected the heading to "VIP-Tg" with capital letters in Figure 1c.

- Figure 1d: The finding that no change was observed in the percentage of VIP+/CR+ is based on three animals and 3-4 slices per mouse. However, the result of VIP+CR+ in tg-mice has an outlier that might bias the results. I would suggest increasing the number of animals to confirm these results.

Thank you for your insightful suggestion. We addressed the potential impact of the outlier in the VIP+/CR+ cell density analysis by recalculating the results after removing the outlier using the interquartile range method. This reanalysis revealed a statistically significant difference in the VIP+/CR+ cell density between non-Tg and Tg mice, which we have now detailed in the Results section. Despite this, we have chosen to retain the outlier in our final presentation to accurately represent the biological variability observed in our sample. We agree that increasing the number of animals would further validate these findings and will consider this in future studies.

- Figure 3d: Would it be possible to identify the recorded interneurons? Is it expected that most of those are OLM cells?

Thank you for your question. We were unable to fully recover all recorded cells using biocytin staining. However, for those cells with preserved axonal structures, we identified both OLM and bistratified cells, which are the primary targets of I-S3 cells. We have now included this information in the Results section to clarify the types of interneurons identified.

- Figure 3: Why quantify VGat terminals instead of quantification of VIP-GFP terminals? Combined with the Calretinine labeling it would be more useful to indicate that no changes were observed at the morphological bouton level specifically in disinhibitory interneurons. Please also describe which imageJ plugin was used for the quantification.

Thank you for your question. Our primary objective was to quantify the synaptic terminals of CR+ INs in the CA1 O/A region, which are predominantly formed by I-S3 cells. Therefore, VGaT and CR co-localization was used to guide this analysis. GFP expression in axonal boutons can sometimes be inconsistent and less reliable for precise quantification. For this analysis, we utilized the “Analyze Particles” function in ImageJ, combined with watershed segmentation, which is now specified in the Methods section.

-  Figure 4g: How was the statistical test performed? If data was averaged across mice, please add error bars and data points in the figure.

Thank you for your question. To compare the alternation percentage between non-Tg and Tg mice, we used Fisher’s Exact test as detailed in Supplementary Table 1. In this analysis, we considered each animal's choice individually, comparing the preference for correct versus incorrect choices between the two groups. Since Fisher’s Exact test is designed for analyzing qualitative data rather than quantitative data, averaging across mice was not applicable, and therefore, we did not include error bars or data points in the figure.

- Figure 4h: To conclude that the increase in activity is larger in the 3xTg mice, there should be a statistical comparison for the magnitude of change between the decision and the stem zone for control and 3xTg mice. To show that there is no significant difference in this measurement in the control mice is insufficient.

Thank you for your suggestion. We performed a statistical comparison of the magnitude of change in activity between the stem zone and the D-zone for non-Tg and 3xTg mice, as recommended. Our analysis showed no significant difference in this magnitude of change between the two genotypes. These results have now been included in the Results section. However, we would like to highlight an important finding regarding the nature of these changes. In the 3xTg mice, there was a consistent increase in the activity of O/A INs when entering the Dzone. In contrast, non-Tg mice displayed a range of responses, including both increases and decreases in activity. This indicates a higher reliability in the firing of O/A INs in the D-zone of 3xTg mice. Our recent study suggests that VIP-INs are particularly active in the D-zone (Tamboli et al., 2024). Therefore, the absence or reduced input from VIP-INs in 3xTg mice may lead to the observed higher engagement of O/A INs in this zone. We believe this observation is crucial for understanding the differential yet nuanced changes in neural dynamics in these mice.

- In the methods, it is stated that there was a pre-selection of animals depending on learning performance. Would it be possible to also show the data from animals that did not properly learn? Alternatively, it would be useful to plot the correlation between performance in this test and the difference between activity in the stem and the decision-making zone. The reason to ask for this is that there is a trend for control animals to show reduced alternations (50 vs 80%, although not significant, it is a big difference). Considering that there is also a trend in control animals to show increased activity in the decision-making zone, it would be important to confirm that this is not only due to differences in performance. The current statistical procedure does not allow discarding this.

In this study, we excluded from the analysis the animals that refused to explore the T-maze and spent all their time in the stem corner, or refused to explore the objects and stayed in the open field maze (OFM) corner. These exclusions applied to both non-Tg (n = 6) and Tg (n = 5) groups, indicating that low exploratory activity is not necessarily linked to AD-related mutations. During the T-maze test, we also observed several animals that made incorrect choices (4 out of 9 non-Tg and 1 out of 6 Tg mice). However, due to the low number of animals making incorrect choices, we were unable to form a separate group for analysis based on incorrect choices. These details are now provided in the Methods section.

- Figure 4i. It is not clear when exactly cell activity was measured. If it was during the entire recording time, I think it would be interesting to see if the activity of O/A interneurons is different specifically during interaction with the object in 3xTg mice.

Cell activity was indeed measured throughout the entire recording session and analyzed in relation to animal behavior (immobility to walking; Fig. 4d,e), and periods specifically related to interaction with objects were extracted for analysis (Figure 4i).

- Why was the object modulation measured during a different task in which both objects were the same? The figure is misleading in that sense, as it suggests the experiment was the same as for the other panels with two different objects. It would be important to correct this if the authors want to correlate the deficits in NOR in 3xTg mice and changes in IN activity.

The study specifically investigated object-modulated neural activity during the Sampling phase. Therefore, two identical objects were placed in the arena for animal exploration. As mentioned above, due to several animals failing to explore the OFM and objects on the second day, they were excluded from the analysis, preventing the conduct of the novel-object exploration Test Trial. Both non-Tg and Tg mice showed a lack of exploration in the OFM and Tmaze, for reasons that remain unclear. Consequently, we opted to present robust data on neural activity during the initial sampling of two identical objects. However, further investigation is needed to understand how this activity relates to deficits observed in the classical NOR test.

- Figure. 5c-f. I would strongly suggest performing the same quantification and displaying similar figures for the fiber photometry experiments in interneurons and principal cells. It would help to interpret the data.

We have taken the reviewer's suggestion into account and standardized the data analysis and presentation. Figures 4d, e and 5c, d now depict the walk-induced activity in INs and PCs, respectively. Figures 4h and 5f compare activity between the stem and D-zone in the T-maze. Additionally, Figures 4j and 5h illustrate the object modulation of INs and PCs, respectively.

- Although velocity and mobility were quantified, it would be important to show also that they are not different during those times when activity was dissimilar, as in the decision zone.

We have analyzed these data and found no significant differences between the two genotypes in terms of velocity and mobility during these periods. This analysis is now presented in Supplementary Figure 5e, f and detailed in the Results section.

- Figure 5g-h. Similarly, I would suggest using the same metrics in order to correlate the results from interneuron and principal cell activity photometry.

We have updated this figure to align with the presentation of interneurons (Figure 4j) and included RMS analysis to emphasize lower variance in object modulation of PCs as an indicator of increased network inhibition.

- Was object modulation variance also different for INs depending on the mouse phenotype?

We conducted this additional analysis but did not find any significant difference.

- Figure S4: would it be possible to identify the postsynaptic partners?

As mentioned above, for those cells with preserved axonal structures, we identified both OLM and bistratified cells. We have now included this information in the Results section to clarify the types of interneurons identified.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

In this study, the authors address a fundamental unresolved question in cerebellar physiology: do synapses between granule cells (GCs) and Purkinje cells (PCs) made by the ascending part of the axon (AA) have different synaptic properties from those made by parallel fibers? This is an important question, as GCs integrate sensorimotor information from numerous brain areas with a precise and complex topography.

Summary:

The authors argue that CGs located close to PCs essentially contact PC dendrites via the ascending part of their axons. They demonstrate that joint high-frequency (100 Hz) stimulation of distant parallel fibers and local CGs potentiates AA-PC synapses, while parallel fiber-PC synapses are depressed. On the basis of paired-pulse ratio analysis, they concluded that evoked plasticity was postsynaptic. When individual pathways were stimulated alone, no LRP was observed. This associative plasticity appears to be sensitive to timing, as stimulation of parallel fibers first results in depression, while stimulation of the AA pathway has no effect. NMDA, mGluR1 and GABAA receptors are involved in this plasticity.

Strengths:

Overall, the associative modulation of synaptic transmission is convincing, and the experiments carried out support this conclusion. However, weaknesses limit the scope of the results.

Weaknesses:

One of the main weaknesses of this study is the suggestion that high-frequency parallel-fiber stimulation cannot induce long term potentiation unless combined with AA stimulation. Although we acknowledge that the stimulation and recording conditions were different from those of other studies, according to the literature (e.g. Bouvier et al 2016, Piochon et al 2016, Binda et al, 2016, Schonewille et al 2021 and others), high-frequency stimulation of parallel fibers leads to long-term postsynaptic potentiation under many different experimental conditions (blocked or unblocked inhibition, stimulation protocols, internal solution composition). Furthermore, in vivo experiments have confirmed that high-frequency parallel fibers are likely to induce long-term potentiation (Jorntell and Ekerot, 2002; Wang et al, 2009).

This article provides further evidence that long-term plasticity (LTP and LTD) at this connection is a complex and subtle mechanism underpinned by many different transduction pathways. It would therefore have been interesting to test different protocols or conditions to explain the discrepancies observed in this dataset.

Even though this is not the main result of this study, we acknowledge that the control experiments done on PF stimulation add a puzzling result to an already contradictory literature. High frequency parallel fibre stimulation (in isolation) has been shown to induce long term potentiation in vitro, but not always, and most importantly, this has been shown in vivo. This was the reason for choosing that particular stimulation protocol. Examination of in vitro studies, however, show that the results are variable and even contradictory. Most were done in the presence of GABAA receptor antagonists, including the SK channel blocker Bicuculline, whereas in the study by Binda (2016), LTP was blocked by GABAA receptor inhibition. In some studies also, LTP was under the control of NMDAR activation only, whereas in Binda (2016), it was under the control of mGluR activation. Moreover, most experiments were done in mice, whereas our study was done in rats. Our results reveal multiple mechanisms working together to produce plasticity, which are highly sensitive to in vitro conditions. We designed our experiments to be close to the physiological conditions, with inhibition preserved and a physiological chloride gradient. It is likely that experimental differences have given rise to the variability of the results and our inability to reproduce PF-LTP, but it was not the aim of this study to dissect the subtleties of the different experimental protocols and models.

We have modified the Discussion to cover that point fully.

Another important weakness is the lack of evidence that the AAs were stimulated. Indeed, without filling the PC with fluorescent dye or biocytin during the experiment, and without reconstructing the anatomical organization, it is difficult to assess whether the stimulating pipette is positioned in the GC cluster that is potentially in contact with the PC with the AAs. According to EM microscopy, AAs account for 3% of the total number of synapses in a PC, which could represent a significant number of synapses. Although the idea that AAs repeatedly contact the same Purkinje cell has been propagated, to the best of the review author's knowledge, no direct demonstration of this hypothesis has yet been published. In fact, what has been demonstrated (Walter et al 2009; Spaeth et al 2022) is that GCs have a higher probability of being connected to nearby PCs, but are not necessarily associated with AAs.

We fully agree with the reviewer that we have not identified morphologically ascending axon synapses, and we stress this fact both in the first paragraph of the Results section, and again at the beginning of Discussion. Our point is mainly topographical, given the well documented geometrical organisation of the cerebellar cortex. Strictly speaking, inputs are local (including AAs) or distal (PFs). Similarly, the studies by Isope and Barbour (2002) and Walter et al. (2009), just like Sims and Hartell (2005 and 2006), have coined the term ‘ascending axon’ when drawing conclusions about locally stimulated inputs. Moreover, our results do not rely on or assume multiple contacts, stronger connections, or higher probability of connections between ascending axons and Purkinje cells. Our results only demonstrate a different plasticity outcome for the two types of inputs. Therefore, our manuscript could be rephrased with the terms ‘local’ and ‘distal’ granule cell inputs, but this would have no more implication for the results or the computation performed in Purkinje cells. However, in our experience, these terms are more confusing, and consistent with the literature, we do not wish to make this modification. However, we have modified the abstract of the manuscript to clarify this point.

Reviewer #2 (Public Review):

Summary:

The authors describe a form of synaptic plasticity at synapses from granule cells onto Purkinje cells in the mouse cerebellum, which is specific to synapses proximal to the cell body but not to distal ones. This plasticity is induced by the paired or associative stimulation of the two types of synapses because it is not observed with stimulation of one type of synapse alone. In addition, this form of plasticity is dependent on the order in which the stimuli are presented, and is dependent on NMDA receptors, metabotropic glutamate receptors and to some degree on GABAA receptors. However, under all experimental conditions described, there is a progressive weakening or run-down of synaptic strength. Therefore, plasticity is not relative to a stable baseline, but relative to a process of continuous decline that occurs whether or not there is any plasticity-inducing stimulus.

As highlighted by the reviewer, we observed a postsynaptic rundown of the EPSC amplitude for both input pathways. Rundown could be mistaken for a depression of synaptic currents, not for a potentiation, and the progressive decrease of the EPSC amplitude during the course of an experiment leads to an underestimate of the absolute potentiation. We have taken the view to provide a strong set of control data rather than selecting experiments based on subjective criteria or applying a cosmetic compensation procedure. We have conducted control experiments with no induction (n = 17), which give a good indication of the speed and amplitude of the rundown. Comparison shows a highly significant potentiation of the ascending axon EPSC. Depression of the parallel fibre EPSC, on the other hand, was not significantly different from rundown, and we have not spoken of parallel fibre long term depression. The data show thus very clearly that ascending axon and parallel fibre synapses behave differently following the costimulation protocol.

Strengths:

The focus of the authors on the properties of two different synapse-types on cerebellar Purkinje cells is interesting and relevant, given previous results that ascending and parallel fiber synapses might be functionally different and undergo different forms of plasticity. In addition, the interaction between these two synapse types during plasticity is important for understanding cerebellar function. The demonstration of timing and order-dependent potentiation of only one pathway, and not another, after associative stimulation of both pathways, changes our understanding of potential plasticity mechanisms. In addition, this observation opens up many new questions on underlying intracellular mechanisms as well as on its relevance for cerebellar learning and adaptation.

Weaknesses and suggested improvements:

A concern with this study is that all recordings demonstrate "rundown", a progressive decrease in the amplitude of the EPSC, starting during the baseline period and continuing after the plasticity-induction stimulus. In the absence of a stable baseline, it is hard to know what changes in strength actually occur at any set of synapses. Moreover, the issues that are causing rundown are not known and may or may not be related to the cellular processes involved in synaptic plasticity. This concern applies in particular to all the experiments where there is a decrease in synaptic strength.

We have provided an answer to that point directly below the summary paragraph. We will just add here that if the phenomenon causing rundown was involved in plasticity, it should affect plasticity of both inputs, which was not the case, clearly distinguishing the ascending axon and parallel fibre inputs.

The authors should consider changes in the shape of the EPSC after plasticity induction, as in Fig 1 (orange trace) as this could change the interpretation.

Figure 1 shows an average response composed of evoked excitatory and inhibitory synaptic currents. The third section of Supplementary material (supplementary figure 3) shows that this complex shape is given by an EPSC followed by a delayed disynaptic IPSC. We would like to point out that while separating EPSC from IPSC might appear difficult from average traces due to the averaged jitter in the onset of the synaptic currents, boundaries are much clearer when analysing individual traces. In the same section we discuss the results of experiments in which transient applications of SR 95531 before and after the induction protocol allowed us to measure the EPSC, while maintaining the same experimental conditions during induction. Analysis of the kinetics of the EPSCs during SR application at the beginning and end of experiments, showed that there is no change in the time to peak of both AA and PF response. The decay time of AA- and PF-EPSCs are slightly longer at the end of the experiment, even if the difference is not significant for AA inputs. This analysis has been added to the Supplementary material. Our analysis, that uses as template the EPSCs kinetics measured at the beginning and at the end of the experiments, takes directly into account these changes. The results show clearly that the presence of disynaptic inhibition doesn’t significantly affect the measure of the peak EPSC after the induction protocol nor the estimate of plasticity.

In addition, the inconsistency with previous results is surprising and is not explained; specifically, that no PF-LTP was induced by PF-alone repeated stimulation.

In our experimental conditions, PF-LTP was not induced when stimulating PF only, the condition that reproduces experiments in the literature. As discussed in our response to reviewer 1, a close look at the literature, however, reveals variabilities and contradictions behind seemingly similar results. They reveal intricate mechanisms working together to produce plasticity, which are sensitive to in vitro conditions. We designed our experiments to be close to physiological conditions, with inhibition preserved and a physiological chloride gradient. It is likely that experimental differences have given rise to the variability of the results and our inability to observe PF-LTP. We have modified the Discussion section to cover that point thoroughly in the context of past results. 

The authors test the role of NMDARs, GABAARs and mGluRs in the phenotype they describe. The data suggest that the form of plasticity described here is dependent on any one of the three receptors. However, the location of these receptors varies between the Purkinje cells, granule cells and interneurons. The authors do not describe a convincing hypothetical model in which this dependence can be explained. They suggest that there is crosstalk between AA and PF synapses via endocannabinoids downstream of mGluR or NO downstream of NMDARs. However, it is not clear how this could lead to the long-term potentiation that they describe. Also, there is no long-lasting change in paired-pulse ratio, suggesting an absence of changes in presynaptic release.

We suggest in the result section that the transient change in paired pulse ratio (PPR) is linked to a transient presynaptic effect, but there was no significant long term change of the PPR, suggesting that the long term effects observed are linked to postsynaptic changes. We now stress this point in the Results and Discussion sections.

Concerning the involvement of multiple molecular pathways, investigators often tested for the involvement of NMDAR or mGluRs in cerebellar plasticity, rarely both. Here we showed that both pathways are involved. The conjunctive requirement for NMDAR and mGluR activation could easily be explained based on the dependence of cerebellar LTP and LTD on the concentrations of both NO and postsynaptic calcium (Coesman et al., 2004; Safo and Regehr, 2005; Bouvier et al., 2016; Piochon et al., 2016).

We also observed an effect of GABAergic inhibition. GABAergic inhibition was elegantly shown by Binda (2016) to regulate calcium entry together with mGluRs, and control plasticity induction. A similar mechanism could contribute to our results, although inhibition might have additional effects. We have modified the Discussion of the manuscript to clarify the pathways involved in plasticity and added a diagram to highlight the links between the different molecular pathways, potential cross talk mechanisms, and the location of receptors.

Is the synapse that undergoes plasticity correctly identified? In this study, since GABAergic inhibition is not blocked for most experiments, PF stimulation can result in both a direct EPSC onto the Purkinje cell and a disynaptic feedforward IPSC. The authors do address this issue with Supplementary Fig 3, where the impact of the IPSC on the EPSC within the EPSC/IPSC sequence is calculated. However, a change in waveform would complicate this analysis. An experiment with pharmacological blockade will make the interpretation more robust. The observed dependence of the plasticity on GABAA receptors is an added point in favor of the suggested additional experiments.

We did consider that due to long recording times there might be kinetic changes, and that’s the reason why the experiments of Supplementary figure 3 were done with pharmacological blockade of GABAAR with SR, both before and again after LTP induction. The estimate of the amplitude of the EPSC is based on the actual kinetics of the response at both times.

A primary hypothesis of this study is that proximal, or AA, and distal, or PF, synapses are different and that their association is specifically what drives plasticity. The alternative hypothesis is that the two synapse-types are the same. Therefore, a good control for pairing AA with PF would be to pair AA with AA and PF with PF, thereby demonstrating that pairing with each other is different from pairing with self.

Pairing AA with AA would be difficult because stimulation of AA can only be made from a narrow band below the PC and we would likely end up stimulating overlapping sets of synapses. However, Figure 5 shows the effect of stimulating PF and PF, while also mimicking the sparse and dense configuration of the control experiment. It shows that sparse PF do not behave like AA. Sims and Hartell (2006) also made an experiment with sparse PF inputs and observed clear differences between sparse local (AA) and sparse distal (PF) synapses.

It is hypothesized that the association of a PF input with an AA input is similar to the association of a PF input with a CF input. However, the two are very different in terms of cellular location, with the CF input being in a position to directly interact with PF-driven inputs. Therefore, there are two major issues with this hypothesis: 1) how can subthreshold activity at one set of synapses affect another located hundreds of micrometers away on the same dendritic tree? 2) There is evidence that the CF encodes teaching/error or reward information, which is functionally meaningful as a driver of plasticity at PF synapses. The AA synapse on one set of Purkinje cells is carrying exactly the same information as the PF synapses on another set of Purkinje cells further up and down the parallel fiber beam. It is suggested that the two inputs carry sensory vs. motor information, which is why this form of plasticity was tested. However, the granule cells that lead to both the AA and PF synapses are receiving the same modalities of mossy fiber information. Therefore, one needs to presuppose different populations of granule cells for sensory and motor inputs or receptive field and contextual information. As a consequence, which granule cells lead to AA synapses and which to PF synapses will change depending on which Purkinje cell you're recording from. And that's inconsistent with there being a timing dependence of AA-PF pairing in only one direction. Overall, it would be helpful to discuss the functional implications of this form of plasticity.

We do not hypothesise that association of the AA and PF inputs is similar to the association of PF and climbing fibre inputs. We compare them because it is the other known configuration triggering associative plasticity in Purkinje cells. It is indeed interesting to observe that even if the inputs are very small compared to the powerful climbing fibre input, they can be effective at inducing plasticity. Physiologically, the climbing fibre signal has been linked to error and reward signals, but reward signals are also encoded by granule cell inputs (Wagner et al., 2017). We have modified the discussion to make sure that we do not suggest equivalence with CF induced LTD.

Moreover, we fully agree that AA and PF synapses made up by a given granule cell carry the same information, and cannot encode sensory and motor information at the same time. AA synapses from a local granule cell deliver information about the local receptive field, but PF synapses from the same granule cell will deliver contextual information about that receptive field to distant Purkinje cells. In the context of sensorimotor learning, movement is learnt with respect to a global context, not in isolation, therefore learning a particular association must be relevant. The associative plasticity we describe here could help explain this functional association. We have clarified the discussion.

Reviewer #3 (Public Review):

Granule cells' axons bifurcate to form parallel fibers (PFs) and ascending axons (AAs). While the significance of PFs on cerebellar plasticity is widely acknowledged, the importance of AAs remains unclear. In the current paper, Conti and Auger conducted electrophysiological experiments in rat cerebellar slices and identified a new form of synaptic plasticity in the AA-Purkinje cell (PC) synapses. Upon simultaneous stimulation of AAs and PFs, AA-PC EPSCs increased, while PFs-EPSCs decreased. This suggests that synaptic responses to AAs and PFs in PCs are jointly regulated, working as an additional mechanism to integrate motor/sensory input. This finding may offer new perspectives in studying and modeling cerebellum-dependent behavior. Overall, the experiments are performed well. However, there are two weaknesses. First, the baseline of electrophysiological recordings is influenced significantly by run-down, making it difficult to interpret the data quantitatively. The amplitude of AA-EPSCs is relatively small and the run-down may mask the change. The authors should carefully reexamine the data with appropriate controls and statistics. Second, while the authors show AA-LTP depends on mGluR, NMDA receptors, and GABA-A receptors, which cell types express these receptors and how they contribute to plasticity is not clarified. The recommended experiments may help to improve the quality of the manuscript.

As highlighted by the reviewer and developed above in response to reviewer 2, we observed a postsynaptic rundown of the EPSC amplitude. Rundown could be mistaken for a depression of synaptic currents, not for a potentiation. Moreover, we have conducted control experiments with no induction (n = 17), which give a good indication of the speed and amplitude of the rundown, and provide a baseline. Comparison shows a highly significant potentiation of the ascending axon EPSC, relative to baseline and relative to these control experiments. Depression of the parallel fibre EPSC on the other hand was not significantly different from rundown. For that reason we have not spoken of parallel fibre long term depression. The data, however, show that ascending axon and parallel fibre synapses behave very differently following the costimulation protocol.

We have discussed above in our response to reviewer 2 the potential involvement of mGluRs, NMDARs and GABAARs. We have clarified the discussion of the pathways involved in plasticity and added a diagram to highlight the links between the different molecular pathways, potential cross talk mechanisms, and the location of receptors.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

- If Chloride concentration cannot be modified, recordings should be performed at the Chloride reversal potential to avoid strong bias in amplitude measurements (e.g. in Figures 3 and 5 outward current was observed while not visible in Figures 1 and 4.

The balance between excitation and inhibition dictates whether there is a visible outward component, and this varies with the connections tested. Careful control experiments with SR application presented in supplementary figure 3 show that the delay of the IPSC does not significantly affect measurement of the peak amplitude of the EPSC. The reversal potential for Clin our study (-85 mV), chosen to reproduce the physiological gradient in Purkinje cells, is too low to record from Purkinje cells at this potential in good conditions as it activates the hyperpolarisation activated cation current Ih, generating huge inward currents.

- It is not clear whether, during the current clamp, the potential was maintained at -65 mV throughout the induction protocol.

The potential was set and maintained around -65mV during the induction protocol. The method section has been amended to specify that point.

- Experiments using GABAB or endocannabinoid antagonists would have been interesting to assess the role of presynaptic plasticity occluding postsynaptic plasticity.

We are not sure why the reviewer suggested these particular experiments to test for the role of presynaptic plasticity. GABAB and endocannabinoid receptor activation both have presynaptic effects at granule cell to Purkinje cell synapses. They decrease release probability, and as a result increase the paired pulse ratio (Dittman and Regehr, 1997; Safo and Regehr, 2005). Here we only observed a transient decrease of the paired pulse ratio. Additionally, presynaptic endocannabinoid receptor activation, linked to postsynaptic mGluR1 activation and release of endocannabinoids, was shown to be required for induction of postsynaptic PF-LTD (Safo and Regehr, 2005). This effect required climbing fibre stimulation and mGluR activation. Here we show that mGluR1 inhibition did not inhibit the PF depression nor affect the transient change in PPR. Therefore there is no indication that activation of these receptors could induce a pre-synaptic depression occluding postsynaptic plasticity.

- To give credit to this new plasticity in contradiction with many previous studies, induction pathways should be addressed more deeply.

As developed earlier in response to the public review, this study does not contradict previous studies, expect maybe that by Binda et al., (2016), conducted on mice. From our point of view, our study in fact reconciles past results which have alternatively involved the mGluR or NMDAR pathways, whereas the molecular downstream pathways they recruit can easily cooperate. We aim to describe a new phenomenon and we cannot cover the mechanistic dissection which has been performed to date on plasticity in the cerebellar cortex.

- The quality of the figures could be enhanced by modifying the dashed line.

We have made the dashed line more discrete.

Reviewer #2 (Recommendations For The Authors):

- Is there cross-talk between the two synaptic pathways?

In order to explain the associative nature of AA-LTP we suggest that a signal is generated at the AA input during the induction protocol only when the PF input is also stimulated, i.e. a form of cross-talk takes place between the two synaptic territories. We have not tested for cross-talk during control conditions but we discuss the fact that given the size of the Purkinje cell dendritic tree, the size of the inputs and their geometrical configuration, it is highly unlikely. We discuss possible cross-talk mechanisms.

- Clarification question: "While the peak amplitude of the first response in the pair of stimulations showed a progressive decline, the peak amplitude of the second response of both AA and PF underwent either LTP or LTD respectively..." Does this mean that all LTP/LTD figures show the amplitude of the second EPSC in the paired pulse stimulation, and that the first EPSC has a different response? If so, this should be mentioned in the Methods section and implications discussed.

All figures show both the amplitude of the first and second EPSCs in the pair of stimulations. In Figure 1A, 3A, 4A and 5B the paired stimulation protocol is depicted with colours and symbols used in the associated graphs, with closed symbols for the first and open symbols for the second EPSC. Figure legends have been amended to clarify this point. The average values given in the Results section and figure legends relate to the first EPSC only for clarity. As can be seen from the figures, long term plasticity affected the first and second EPSC in a very similar manner. However, individual symbols show that during a transient period, the first and second EPSCs are differentially affected by the induction protocol, resulting in a transient change of the PPR.

Minor suggestions:

- It would be helpful to have a reference for the statement that 1-2% of stimulated fibers come from nearby GCs when stimulation is distal.

We have modified the text to explain our calculation based on the data of Pichitpornchai et al., 1994. P4 result section.

- Does the shading over the plasticity time course traces come from the standard error of the mean?

Shading over the plasticity time course plots shows the standard error of the mean. This is now clearly stated in figure legends.

Reviewer #3 (Recommendations For The Authors):

Major points:

(1) Whether the plasticity between AAs and PCs is regulated by the post-synaptic or pre-synaptic mechanisms should be addressed or discussed. Based on the results of PPR (mostly unchanged after induction), the post-synaptic mechanism may be more significant. Supplemental Figure 2C shows a trend toward a positive correlation between AALTP and the number of spikes, suggesting intracellular calcium levels in the post-synaptic Purkinje cells may be important. Whether this is true or not can be directly tested by the addition of BAPTA in the recording pipettes.

The absence of a long lasting effect on the paired pulse ratio (PPR) indicates that postsynaptic mechanisms are involved in long term changes. This is in line with the dependence of plasticity induced with similar protocols on the concentrations of NO and postsynaptic calcium, both affecting postsynaptic targets, as developed in our response to reviewer 2. BAPTA interferes with calcium and mGluR signalling, and could be used to further confirm the involvement of a postsynaptic mechanism, however, we did not wish to pursue further the dissection of the signalling cascade. We have modified the Results and Discussion sections to include a discussion of pre and postsynaptic mechanisms.

(2) Most results from the plasticity experiments are shown as average/sem and do not include individual data, making ithard to appreciate the magnitude of the changes. The authors could show the individual data at some time points (e.g. 5 min before and 30 min after induction), plot bar-graphs (Figure 2C with individual data), or boxplots to compare different conditions and perform statistics.

Individual data points are now visible for plasticity induction in Figure 2C and Supplementary Figure 2 for a number of conditions. Statistics have been performed as detailed in the text and legend of Fig 2.

(3) In addressing point #2, it is strongly recommended that the authors include the values for controls without inductionbecause AA/PF-EPSCs undergo significant run-down. In most experiments, the authors compare the magnitude of plasticity with baseline changes in Supplemental Figure 1. This should not be appropriate for some experiments, such as Figures 3 & 4, where pharmacological treatments are performed. The authors should carefully consider including the appropriate controls from baseline recording to rule out significant confound by the run-down.

We agree that control experiments without stimulation (no Stim) are only appropriate controls for the initial synchronous stimulation and AA and PF only experiments (Fig 1). All the other experiments were compared to the synchronous stimulation experiments, not to control No Stim. The synchronous stimulation protocol is strictly the same as that applied in experiments with pharmacological treatments and the appropriate control to test whether treatments affected plasticity. This is now systematically specified in the Results section.

(4) The authors recorded mixed EPSC/IPSCs and used a fitting approach to extract EPSCs. Applying AMPA-receptor blockers to check that extracted IPSCs are correctly predicted may solidify the reliability of the approach. An additional concern is that this approach can only be used if the waveform of EPSC/IPSC does not change with plasticity. The authors should compare the waveforms between conditions to address this point.

Fits were not used to extract EPSCs. EPSCs were isolated by blocking IPSCs with SR95531, and the IPSCs were then extracted by subtraction from the mixed EPSC/IPSC. Fits were then done of the isolated EPSC and the extracted IPSC. This procedure was applied both at the start of the experiment and at the end to avoid changes in kinetics that would influence measurements. A section of supplementary material is devoted to this analysis. Isolating IPSCs using AMPAR blockers is not possible as IPSCs are disynaptic. AMPAR blockers would fully suppress inhibition.

(5) While the AA-LTP depends on NMDA-Rs, which cell type is responsible is not clear. Recording NMDA components in AA/PF-EPSCs should be informative in addressing this point. Cesana et al suggested that AA induces significant activation of NMDA-Rs in Golgi cells (PMID: 23884948). Whether AA stimuli could significantly evoke NMDA current in the experimental condition used in this paper could provide essential information.

The granule cell to Purkinje cell EPSCs are devoid of an NMDAR component (Llano et al., 1991), and there is no postsynaptic NMDARs at granule cell to PC synapses, but a proportion of presynaptic boutons show the presence of NMDARs (Bidoret et al, 2009). This is now stated clearly on p8.  Presynaptic NMDAR have been involved in LTP and LTD of parallel fibre synapses (Casado et al., 2002; Bouvier et al., 2016; Schonewille et al., 2021), and linked to the activation of NOS in granule cell axons. However, we do not know whether presynaptic NMDARs are also present at AA synapses. NMDAR and NOS are also expressed by molecular layer interneurons, and have sometimes been involved in LTD induction (Kono et al., 2019), although this is disputed. In the paper by Cesana (2013), white matter stimulation activated mossy fibre inputs to granule cells, and as a consequence, granule cell to Golgi cell disynaptic EPSCs. The authors identified AA synapses on the basolateral dendrites of Golgi cells, and showed NMDAR activation associated with the mossy fibre to granule cell EPSC. Granule cell to Golgi cell synapses were shown to activate both postsynaptic AMPA and NMDA receptors (Dieudonné, 1999). But to our knowledge, Golgi cells do not express NOS. Therefore it is unlikely that activation of NMDARs in Golgi cells is linked to synaptic plasticity in Purkinje cells.

(6) Pharmacological experiments in Figure 3 show that AA-LTP is dependent on mGluR. The authors mentioned that it could be explained by the presence and absence of mGluRs in PFs and AAs, respectively. This is an important and reasonable possibility and should be tested. The authors could simply check whether slow EPSCs can be recorded by the AA activation.

Activation of the mGluR slow EPSC by AA stimulation would reveal the presence of mGluRs at AA inputs. We know, however, that sparse PF stimulation does not activate the mGluR slow EPSC nor endocannabinoid release unless glutamate transporters are blocked (Marcaggi and Attwell., 2005). This is thought to reflect insufficient glutamate buildup in the sparse configuration to activate mGluR1s. AA inputs are sparsely distributed and are not expected to activate the slow EPSC either, and this is confirmed by our own experiments (CA personal communication). However, mGluR1 mediated Ca2+ release from stores shows a higher sensitivity to glutamate than the slow EPSC (Canepari and Ogden, 2006) and might take place with sparse inputs, but Ca2+ signals have not been investigated in this configuration. Therefore the absence of the slow EPSC is not sufficient proof that mGluR1s are not activated and not present at AA synapses. This is now further discussed p12.

Minor points:

(1) The authors should describe how they adjusted the stimulation strength for both AAs and PFs.

Adjustment of the stimulation intensity is now described in the Methods section.

(2) A rationale explaining why the authors chose the current induction protocol (synchronous stimulation of both inputs) should be included. This will help the readers to understand the background of the study.

Papers by Sims and Hartell (2005, 2006) and experimental evidence indicated that AA and PF inputs may have different properties, and as a result may play different roles. Moreover, based on the morphology of the cerebellar granule cell and Purkinje cell, AA and PF inputs can carry different information to a given Purkinje cell. We reasoned that co-presentation of the inputs might represent an important piece of information for the circuit, signalling functional association, and lead to plasticity, as seen for motor command and sensory feedback in cerebellar-like structures, or for PF and climbing fibre. We have tried to convey that rational in the abstract and introduction.

(3) Supplemental Figure 2B: the x-axis may be labeled incorrectly, Is the x-axis of the top graph for PF PF-EPSC? Thex-axis for the bottom graphs should be the summation of AA- and PF-EPSCs.

This has been corrected.

(4) "mglur1" on page 10 should be mGluR1.

This has been corrected.

Author response:

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

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Please reorder the supplementary figures in the order they are referred to in the Results section for ease of reading. Supp Fig 5 b - should read 'Mean normalized fluorescence of LC ROIs (n = 87) during immobile periods aligned to the switch from familiar to novel environment.’

We thank the reviewer for highlighting these issues and have reordered the supplementary figures and edited the figure legends appropriately.

Reviewer #2 (Recommendations For The Authors):

The authors should include sample size justifications (e.g. based on previous studies, considerations of statistical power, practical considerations, or a combination of these factors).

In response to this concern, we have added a statement to the “Imaging Sessions” section of the methods. Here we highlight sample sizes were largely based on previous studies and/or limited by the difficulty of recordings and the limited number of visible axons per imaging session.

Reviewer #3 (Recommendations For The Authors):

The addition of Supp. Fig 5 partially addresses my previous point 3. However, the claim of dissociation between VTA-CA1 and LC-CA1 would be strengthened by showing that VTA-CA1 axons do not respond to the darkness -> familiar environment in Supp Fig 5. This is particularly important given that (1) the additional 2 VTA-CA1 axons in the revision were not recorded during transitions to novel environments and (2) the overall concern of the reviewers that the low n and heterogeneity of the VTA-CA1 dataset may lead to a false negative. Providing VTA-CA1 data for the darkness -> familiar environment would provide a within-manuscript replication that these axons are not responding to environment changes; a major claim of this manuscript.

While we agree that data of VTA-CA1 axons during the switch from darkness to the familiar environment would provide additional evidence that these axons are not responding to environment changes, unfortunately, VTA axons were not recorded during the switch from familiar to novel.

Author response:

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

eLife assessment 

The authors present 16 new well-preserved specimens from the early Cambrian Chengjiang biota. These specimens potentially represent a new taxon which could be useful in sorting out the problematic topology of artiopodan arthropods - a topic of interest to specialists in Cambrian arthropods. Because the anatomic features in the new specimens were neither properly revealed nor correctly interpreted, the evidence for several conclusions is inadequate. 

We thank the Senior Editor, Reviewing Editor and three reviewers for their work, and for their comments aimed at improving this project and manuscript. We have engaged with all the comments in detail, in order to strengthen our work. This includes adding additional data to support that all Acanthomeridion specimens belong to a single species, running further phylogenetic analyses including more trilobite terminals to test the specific hypothesis and interpretation raised by Reviewer 2, and visualising our results in treespace in order to determine support for the different interpretations of the ventral structures and their implications for the evolution of Artiopoda. We have also greatly expanded the introduction, which we feel adds clarity to areas misunderstood by some reviewers in the previous version of the manuscript.

Our point-by-point response to the public reviews of the reviewers are outlined below. We have also made changes resulting from the additional suggestions which are not public, which we have not reproduced below. We submit a new version of the main text, and can provide a tracked changes version if required. The new main text includes 9 figures and is 8624 words including captions and reference list.

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

Du et al. report 16 new well-preserved specimens of atiopodan arthropods from the Chengjiang biota, which demonstrate both dorsal and ventral anatomies of a potential new taxon of artipodeans that are closely related to trilobites. Authors assigned their specimens to Acanthomeridion serratum and proposed A. anacanthus as a junior subjective synonym of Acanthomeridion serratum. Critically, the presence of ventral plates (interpreted as cephalic liberigenae), together with phylogenic results, lead authors to conclude that the cephalic sutures originated multiple times within the Artiopoda. 

We thank Reviewer 1 for their comments on the strengths and weaknesses of the previous version of the manuscript. We hope that the revised version strengthens our conclusions that Acanthomeridion anacanthus is a junior synonym of A. serratum.

Strengths: 

New specimens are highly qualified and informative. The morphology of the dorsal exoskeleton, except for the supposed free cheek, was well illustrated and described in detail, which provides a wealth of information for taxonomic and phylogenic analyses. 

Weaknesses: 

The weaknesses of this work are obvious in a number of aspects. Technically, ventral morphology is less well revealed and is poorly illustrated. Additional diagrams are necessary to show the trunk appendages and suture lines. Taxonomically, I am not convinced by the authors' placement. The specimens are markedly different from either Acanthomeridion serratum Hou et al. 1989 or A. anacanthus Hou et al. 2017. The ontogenetic description is extremely weak and the morpholical continuity is not established. Geometric and morphometric analyses might be helpful to resolve the taxonomic and ontogenic uncertainties. 

We appreciate that the reviewer was not convinced by our synonimisation in the first version of the manuscript. The recommendation of the reviewer to provide linear morphometric support for our synonymisation was much appreciated. We have provided measurements of the length and width of the thorax (Figure 6 in the new version), visualising the position of specimens previously assigned to A. anacanthus, to show this morphological continuity. These act as a complement to Figure 5, which shows the fossils in an ontogenetic trend.

I am confused by the author's description of the free cheek (libragena) and ventral plate. Are they the same object? How do they connect with other parts of the cephalic shield, e.g. hypostome, and fixgena? Critically, the homology of cephalic slits (eye slits, eye notch, dorsal suture, facial suture) is not extensively discussed either morphologically or functionally.

We appreciate that the brevity of the introduction in the previous version led to some misunderstandings and some confusion. We have provided a greatly expanded introduction, including a new Figure 1, which outlines the possible homologies of the ventral plates and the three hypotheses considered in this study. The function of the cephalic and dorsal suture are now discussed in more detail both in introduction and discussion.

Finally, the authors claimed that phylogenic results support two separate origins rather than a deep origin. However, the results in Figure 4 can explain a deep homology of the cephalic suture at molecular level and multiple co-options within the Atiopoda. 

A deep molecular origin is difficult to demonstrate using solely fossil material from an extinct group such as Artiopoda. Thus our study focuses on morphological origins. The number of losses required for a deep morphological origin means that we favour multiple independent morphological origins.

Reviewer #2 (Public Review): 

Overall: This paper describes new material of Acanthomeridion serratum that the authors claim supports its synonymy with Acanthomeridion anacanthus. The material is important and the description is acceptable after some modification. In addition, the paper offers thoughts and some exploration of the possibility of multiple origins of the dorsal facial suture among artiopods, at least once within Trilobita and also among other non-trilobite artiopods. Although this possibility is real and apparently correct, the suggestions presented in this paper are both surprising and, in my opinion, unlikely to be true because the potential homologies proposed with regard to Acanthomeridion and trilobite-free cheeks are unconventional and poorly supported. 

What to do? I can see two possibilities. One, which I recommend, is to concentrate on improving the descriptive part of the paper and omit discussion and phylogenetic analysis of dorsal facial suture distribution, leaving that for more comprehensive consideration elsewhere. The other is to seek to improve both simultaneously. That may be possible but will require extensive effort. 

We thank the reviewer for their detailed comments and suggestions for multiple ways in which we might revise the manuscript. We have taken the option that is more effort, but we hope more reward, in interrogating the larger question alongside improving the descriptive part of the paper. This has taken a long time and incorporation of new techniques, but has in our opinion greatly strengthened the work.

Major concerns 

Concern 1 - Ventral sclerites as free cheek homolog, marginal sutures, and the trilobite doublure 

Firstly, a couple of observations that bear on the arguments presented - the eyes of A. serratum are almost marginal and it is not clear whether a) there is a circumocular suture in this animal and b) if there was, whether it merged with the marginal suture. These observations are important because this animal is not one in which an impressive dorsal facial suture has been demonstrated - with eyes that near marginal it simply cannot do so. Accordingly, the key argument of this paper is not quite what one would expect. That expectation would be that a non-trilobite artiopod, such as A. serratum, shows a clear dorsal facial suture. But that is not the case, at least with A. serratum, because of its marginal eyes. Rather, the argument made is that the ventral doublure of A. serratum is the homolog of the dorsal free cheeks of trilobites. This opens up a series of issues. 

We appreciate that the reviewer disagrees with both interpretations we offered for the ventral plates, and has offered a third interpretation for the homology of this feature with the doublure of trilobites. Support for our original interpretation comes from the position of the eye stalks in Acanthomeridion, which fall very close to the suture between ventral plate rest of the cephalon. However, we appreciate that the reviewer has a valid interpretation, that the ventral plates might be homologues of the doublure alone.

To clarify the (two, now three) hypotheses of homology for the ventral plates considered in this study, we provide a new summary figure (Figure 1). In addition, the introduction has been greatly lengthened with further discussion of the different suture types in trilobites, their importance for trilobite classification schemes, and extensive references to older literature are now included. Further, we add background to the hypotheses around the origins of dorsal ecdysial sutures. 

We add that the interpretation of A. serratum as having features homologous to the dorsal sutures of trilobites is already present in the literature, and so while the reviewer may disagree with it, it is certainly a hypothesis that requires testing.

The paper's chief claim in this regard is that the "teardrop" shaped ventral, lateral cephalic plates in Acanthomeridion serratum are potential homologs of the "free cheeks" of those trilobites with a dorsal facial suture. There is no mention of the possibility that these ventral plates in A. serratum could be homologs of the lateral cephalic doublure of olenelloid trilobites, which is bound by an operative marginal suture or, in those trilobites with a dorsal facial suture, that it is a homolog of only the doublure portions of the free cheeks and not with their dorsal components. 

We include this third possibility in our revised analyses and manuscript. To test this properly required adding in an olenelloid trilobite to our matrix, as we needed a terminal that had both a marginal and circumoral suture, but not fused. We chose Olenellus getzi for this purpose, as it is the only Olenellus with some appendages known (the antennae). We also added further characters to the morphological matrix, and additional trilobites from which soft tissues are known, in order to better resolve this part of the tree. Trilobites in the final analyses were: Anacheirurus adserai, Cryptolithus tesselatus, Eoredlichia intermedia, Olenoides serratus, Olenellus getzi, Triarthrus eatoni.

However, addition of these trilobites added a further complication. Under unconstrained analysis, Olenellus getzi was resolved with Eoredlichia intermediata as a clade sister to all other trilobites.

Thus the topology of Paterson et al. 2019 (PNAS) was not recovered, and so the hypothesis of Reviewer 2 could not be robustly tested. In order to achieve a topology comparable to Paterson et al., we ran a further three analyses, where we constrained a clade of all trilobites except for O. getzi. This recovered a topology where the earliest diverging trilobites had unfused sutures, and thus one suitable for considering the role of Acanthomeridion serratum ventral plates as homologues of the doublure of trilobites.

Unfortunately, for these analyses (both constrained and unconstrained), Acanthomeridion was not resolved as sister to trilobites, but instead elsewhere in the tree (see Table 1 in main text, Fig. 9, and  SFig 9). Thus our analyses do not find support for the reviewer’s hypothesis as multiple origins of this feature are still required.

It was still an excellent point that we should consider this hypothesis, and we have retained it, and discussion surrounding it, in our manuscript.

The introduction to the paper does not inform the reader that all olenelloids had a marginal suture - a circumcephalic suture that was operative in their molting and that this is quite different from the situation in, say, "Cedaria" woosteri in which the only operative cephalic exoskeletal suture was circumocular. The conservative position would be that the olenelloid marginal suture is the homolog of the marginal suture in A. serratum: the ventral plates thus being homolog of the trilobite cephalic doublure, not only potential homolog to the entire or dorsal only part of the free cheeks of trilobites with a dorsal facial suture. As the authors of this paper decline to discuss the doublure of trilobites (there is a sole mention of the word in the MS, in a figure caption) and do not mention the olenelloid marginal suture, they give the reader no opportunity to assess support for this alternative. 

At times the paper reads as if the authors are suggesting that olenelloids, which had a marginal cephalic suture broadly akin to that in Limulus, actually lacked a suture that permitted anterior egression during molting. The authors are right to stress the origin of the dorsal cephalic suture in more derived trilobites as a character seemingly of taxonomic significance but lines such as 56 and 67 may be taken by the non-specialist to imply that olenelloids lacked a forward egressionpermiting suture. There is a notable difference between not knowing whether sutures existed (a condition apparently quite common among soft-bodied artiopods) and the well-known marginal suture of olenelloids, but as the MS currently reads most readers will not understand this because it remains unexplained in the MS. 

As noted in response to a previous point (above) we now have a greatly expanded introduction which should give the reader an opportunity to assess support for this alternative hypothesis. We now include Olenellus getzi in our analyses, and have added characters to the morphological matrix to make this clear.

A reference to the case of ‘Cedaria’ woosteri is made in the introduction to highlight further the variability of trilobites, as is a reference to Foote’s analysis of cranidial shapes and support this provides for a  single origin of the dorsal suture.

With that in mind, it is also worth further stressing that the primary function of the dorsal sutures in those which have them is essentially similar to the olenelloid/limulid marginal suture mentioned above. It is notable that the course of this suture migrated dorsally up from the margin onto the dorsal shield and merged with the circumocular suture, but this innovation does not seem to have had an impact on its primary function - to permit molting by forward egression. Other trilobites completely surrendered the ability to molt by forward egression, and there are even examples of this occurring ontogenetically within species, suggesting a significant intraspecific shift in suture functionality and molting pattern. The authors mention some of this when questioning the unique origin of the dorsal facial suture of trilobites, although I don't understand their argument: why should the history of subsequent evolutionary modification of a character bear on whether its origin was unique in the group? 

We include reference to evolutionary modification and loss of this character as it is important to stress that if a character is known to have been lost multiple times it is possible that it had a deeper root (in an earlier diverging member of Artiopoda than Trilobita) and was lost in olenelloids. This is the question that we seek to address in our manuscript.

The bottom line here is that for the ventral plates of A. serratum to be strict homologs of only the dorsal portion of the dorsal free cheeks, there would be no homolog of the trilobite doublure in A. serratum. The conventional view, in contrast, would be that the ventral plates are a homolog of the ventral doublure in all trilobites and ventral plates in artiopods. I do not think that this paper provides a convincing basis for preferring their interpretation, nor do I feel that it does an adequate job of explaining issues that are central to the subject. 

We stress that our interpretations – that the ventral plates are not homologous to any artiopodan feature or that they are homologous to the free cheeks of trilobites – have both been raised in the literature before. Whereas we could not find mention of the reviewer’s ‘conventional view’ relating to Acanthomeridion. We appreciate that this view is still valid and worth investigating, which we have done in the further analyses conducted. However, we did not find support for it. Instead we find some support for both ventral plates as homologues of free cheeks, and as unique structures within Artiopoda.

Concern 2. Varieties of dorsal sutures and the coexistence of dorsal and marginal sutures 

The authors do not clarify or discuss connections between the circumocular sutures (a form of dorsal suture that separates the visual surface from the rest of the dorsal shield) and the marginal suture that facilitates forward egression upon molting. Both structures can exist independently in the same animal - in olenelloids for example. Olenelloids had both a suture that facilitated forward egression in molting (their marginal suture) and a dorsal suture (their circumocular suture). The condition in trilobites with a dorsal facial suture is that these two independent sutures merged - the formerly marginal suture migrating up the dorsal pleural surface to become confluent with the circumocular suture. (There are also interesting examples of the expansion of the circumocular suture across the pleural fixigena.) The form of the dorsal facial suture has long figured in attempts at higher-level trilobite taxonomy, with a number of character states that commonly relate to the proximity of the eye to the margin of the cephalic shield. The form of the dorsal facial suture that they illustrate in Xanderella, which is barely a strip crossing the dorsal pleural surface linking marginal and circumocular suture, is comparable to that in the trilobites Loganopeltoides and Entomapsis but that is a rare condition in that clade as a whole. The paper would benefit from a clear discussion of these issues at the beginning - the dorsal facial suture that they are referring to is a merged circumcephalic suture and circumocular suture - it is not simply the presence of a molt-related suture on the dorsal side of the cephalon. 

We have added in an expanded introduction where these points are covered in detail. We appreciate that this was not clear in the earlier version, and this suggestion has greatly improved our work.

Concern 3. Phylogenetics 

While I appreciate that the phylogenetic database is a little modified from those of other recent authors, still I was surprised not to find a character matrix in the supplementary information (unless it was included in some way I overlooked), which I would consider a basic requirement of any paper presenting phylogenetic trees - after all, there's no a space limit. It is not possible for a reviewer to understand the details of their arguments without seeing the character states and the matrix of state assignments. 

A link to a morphobank project was included in the first submission. This project has been updated for the current submission, including an additional matrix to treat the reviewer’s hypothesis for the ventral plates. Morphobank Project #P4290. Email address: P4290, reviewer password:

Acanthomeridion2023, accessible at morphobank.org. We have added in additional details for the reviewer and others to help them access the project:

The project can be accessed at morphobank.org, using the below credentials to log in:  Email address: P4290, Password: Acanthomeridion 2023.

The section "phylogenetic analyses" provides a description of how tree topology changes depending on whether sutures are considered homologous or not using the now standard application of both parsimony and maximum likelihood approaches but, considering that the broader implications of this paper rest of the phylogenetic interpretation, I also found the absence of detailed discussion of the meaning and implications of these trees to be surprising, because I anticipated that this was the main reason for conducting these analysis. The trees are presented and briefly described but not considered in detail. I am troubled by "Circles indicate presence of cephalic ecdysial sutures" because it seems that in "independent origin of sutures" trilobites are considered to have two origins (brown color dot) of cephalic ecdysial sutures - this may be further evidence that the team does not appreciate that olenelloids have cephalic ecdysial sutures, as the basal condition in all trilobites. Perhaps I'm misunderstanding their views, but from what's presented it's not possible to know that. Similarly, in the "sutures homologous" analyses why would there be two independent green dots for both Acanthomeridion and Trilobita, rather than at the base of the clade containing them both, as cephalic ecdysial sutures are basal to both of them? Here again, we appear to see evidence that the team considers dorsal facial sutures and cephalic ecdysial sutures to be synonymous - which is incorrect.  

We appreciate that the reviewer misunderstood the meaning of the dots, leading to confusion. The dots indicated how features were coded in the phylogenetic analysis. In our revised version of this figure (Figure 8 in the new version), these dots are now clearly labelled as indicating ‘coding in phylogenetic matrix’. Further, with the revised character list, we now can provide additional detail for the types of sutures (relevant as we now include more trilobite terminals).

This point aside, and at a minimum, that team needs to do a more thorough job of characterizing and considering the variety of conditions of dorsal sutures among artiopods, their relationships to the marginal suture and to the circumocular suture, the number, and form of their branches, etc. 

We thank the reviewer for this summary, and appreciate their concerns and thorough review. Our revised version takes into account all these points raised, and they have greatly improved the clarity, scope and thoroughness of the work.

Reviewer #3 (Public Review): 

Summary:

Well-illustrated new material is documented for Acanthomeridion, a formerly incompletely known Cambrian arthropod. The formerly known facial sutures are shown to be associated with ventral plates that the authors very reasonably homologise with the free cheeks of trilobites. A slight update of a phylogenetic dataset developed by Du et al, then refined slightly by Chen et al, then by Schmidt et al, and again here, permits another attempt to optimise the number of origins of dorsal ecdysial sutures in trilobites and their relatives. 

Strengths:

Documentation of an ontogenetic series makes a sound case that the proposed diagnostic characters of a second species of Acanthomeridion are variations within a single species. New microtomographic data shed some light on appendage morphology that was not formerly known. The new data on ventral plates and their association with the ecdysial sutures are valuable in underpinning homologies with trilobites. 

We thank the Reviewer 3 for their positive comments about the manuscript. We appreciate the constructive comments for improvements, and detailed corrections, which we have incorporated into our revised work.

Weaknesses:

The main conclusion remains clouded in ambiguity because of a poorly resolved Bayesian consensus and is consistent with work led by the lead author in 2019 (thus compromising the novelty of the findings). The Bayesian trees being majority rules consensus trees, optimising characters onto them (Figure 7b, d) is problematic. Optimising on a consensus tree can produce spurious optimisations that inflate tree length or distort other metrics of fit. Line 264 refers to at least three independent origins of cephalic sutures in artiopodans but the fully resolved Figure 7c requires only two origins. 

We thank the reviewer for pointing this out. However now the analyses have been re-run we have new results to consider. The results still support multiple origins of sutures. We also note that the dots were indicating how terminals were coded. This is now clearer in the revised version of this figure (Figure 8 in the new version).

We have extended our interrogation of the trees by incorporating treespace analyses. These add support for the nodes of interest (around the base of trilobites), showing that the coding of Acanthomeridion ventral plate homologies impacts its position in the tree, and thus has implications for our understanding of the evolution of sutures in trilobites.

The question of how many times dorsal ecdysial sutures evolved in Artiopoda was addressed by Hou et al (2017), who first documented the facial sutures of Acanthomeridion and optimised them onto a phylogeny to infer multiple origins, as well as in a paper led by the lead author in Cladistics in 2019. Du et al. (2019) presented a phylogeny based on an earlier version of the current dataset wherein they discussed how many times sutures evolved or were lost based on their presence in

Zhiwenia/Protosutura, Acanthomeridion, and Trilobita. To their credit, the authors acknowledge this (lines 62-65). The answer here is slightly different (because some topologies unite Acanthomeridion and trilobites). 

The following points are not meant to be "Weaknesses" but rather are refinements: 

I recommend changing the title of the paper from "cephalic sutures" to "dorsal ecdysial sutures" to be more precise about the character that is being tracked evolutionarily. Lots of arthropods have cephalic sutures (e.g., the ventral marginal suture of xiphosurans; the Y-shaped dorsomedian ecdysial line in insects). The text might also be updated to change other instances of "cephalic sutures" to a more precise wording. 

We appreciate this point and have changed the title as suggested. 

The authors have provided (but not explicitly identified) support values for nodes in their Bayesian trees but not in their parsimony ones. Please do the jackknife or bootstrap for the parsimony analyses and make it clear that the Bayesian values are posterior probabilities. 

With the addition of further trilobite terminals to our parsimony analyses, the results became poor.

Specifically the internal relationships of trilobites did not conform to any previous study, and Olenellus getzi was not resolved as an early diverging member of the group. This meant that these analyses could not be used for addressing the hypothesis of reviewer two. We decided to exclude reporting parsimony analysis results from this version to avoid confusion.

We have added a note that the values reported at the nodes are posterior probabilities to figures S8, S9 and S10 where we show the full Bayesian results.

In line 65 or somewhere else, it might be noted that a single origin of the dorsal facial sutures in trilobites has itself been called into question. Jell (2003) proposed that separate lineages of Eutrilobita evolved their facial sutures independently from separate sister groups within Olenellina. 

We have added this to the introduction (Line 98). Thank you for raising this point.

I have provided minor typographic or terminological corrections to the authors in a list of recommendations that may not be publicly available. 

We appreciate the points made by the reviewer and their detailed corrections, which we have corrected in the revised version.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

In this paper the authors provide a characterisation of auditory responses (tones, noise, and amplitude modulated sounds) and bimodal (somatosensory-auditory) responses and interactions in the higher order lateral cortex (LC) of the inferior colliculus (IC) and compare these characteristic with the higher order dorsal cortex (DC) of the IC - in awake and anaesthetised mice. Dan Llano's group have previously identified gaba'ergic patches (modules) in the LC distinctly receiving inputs from somatosensory structures, surrounded by matrix regions receiving inputs from auditory cortex. They here use 2P calcium imaging combined with an implanted prism to - for the first time - get functional optical access to these subregions (modules and matrix) in the lateral cortex of IC in vivo, in order to also characterise the functional difference in these subparts of LC. They find that both DC and LC of both awake and anaesthetised appears to be more responsive to more complex sounds (amplitude modulated noise) compared to pure tones and that under anesthesia the matrix of LC is more modulated by specific frequency and temporal content compared to the gaba'ergic modules in LC. However, while both LC and DC appears to have low frequency preferences, this preference for low frequencies is more pronounced in DC. Furthermore, in both awake and anesthetized mice somatosensory inputs are capable of driving responses on its own in the modules of LC, but very little in the matrix. The authors now compare bimodal interactions under anaesthesia and awake states and find that effects are different in some cases under awake and anesthesia - particularly related to bimodal suppression and enhancement in the modules.

The paper provides new information about how subregions with different inputs and neurochemical profiles in the higher order auditory midbrain process auditory and multisensory information, and is useful for the auditory and multisensory circuits neuroscience community.

The manuscript is improved by the response to reviewers. The authors have addressed my comments by adding new figures and panels, streamlining the analysis between awake and anaesthetised data (which has led to a more nuanced, and better supported conclusion), and adding more examples to better understand the underlying data. In streamlining the analyses between anaesthetised and awake data I would probably have opted for bringing these results into merged figures to avoid repetitiveness and aid comparison, but I acknowledge that that may be a matter of style. The added discussions of differences between awake and anaesthesia in the findings and the discussion of possible reasons why these differences are present help broaden the understanding of what the data looks like and how anaesthesia can affect these circuits.

As mentioned in my previous review, the strength of this study is in its demonstration of using prism 2p imaging to image the lateral shell of IC to gain access to its neurochemically defined subdivisions, and they use this method to provide a basic description of the auditory and multisensory properties of lateral cortex IC subdivisions (and compare it to dorsal cortex of IC). The added analysis, information and figures provide a more convincing foundation for the descriptions and conclusions stated in the paper. The description of the basic functionality of the lateral cortex of the IC are useful for researchers interested in basic multisensory interactions and auditory processing and circuits. The paper provides a technical foundation for future studies (as the authors also mention), exploring how these neurochemically defined subdivisions receiving distinct descending projections from cortex contribute to auditory and multisensory based behaviour.

Minor comment:

- The authors have now added statistics and figures to support their claims about tonotopy in DC and LC. I asked for and I think allows readers to better understand the tonotopical organisation in these areas. One of the conclusions by the authors is that the quadratic fit is a better fit that a linear fit in DCIC. Given the new plots shown and previous studies this is likely true, though it is worth highlighting that adding parameters to a fitting procedure (as in the case when moving from linear to quadratic fit) will likely lead to a better fit due to the increased flexibility of the fitting procedure.

Thank you for the suggestion. We have highlighted that the quadratic function allowed the regression model to include the cells tuned to higher frequencies at the rostromedial part of the DC and result in a better fit, which is consistent with the tonotopic organization that was previously described as shown in text at (lines 208-211).

Reviewer #2 (Public Review):

Summary:

The study describes differences in responses to sounds and whisker deflections as well as combinations of these stimuli in different neurochemically defined subsections of the lateral and dorsal cortex of the inferior colliculus in anesthetised and awake mice.

Strengths:

A major achievement of the work lies in obtaining the data in the first place as this required establishing and refining a challenging surgical procedure to insert a prism that enabled the authors to visualise the lateral surface of the inferior colliculus. Using this approach, the authors were then able to provide the first functional comparison of neural responses inside and outside of the GABA-rich modules of the lateral cortex. The strongest and most interesting aspects of the results, in my opinion, concern the interactions of auditory and somatosensory stimulation. For instance, the authors find that a) somatosensory-responses are strongest inside the modules and b) somatosensory-auditory suppression is stronger in the matrix than in the modules. This suggests that, while somatosensory inputs preferentially target the GABA-rich modules, they do not exclusively target GABAergic neurons within the modules (given that the authors record exclusively from excitatory neurons we wouldn't expect to see somatosensory responses if they targeted exclusively GABAergic neurons) and that the GABAergic neurons of the modules (consistent with previous work) preferentially impact neurons outside the modules, i.e. via long-range connections.

Weaknesses:

While the findings are of interest to the subfield they have only rather limited implications beyond it and the writing is not quite as precise as it could be.

Reviewer #3 (Public Review):

The lateral cortex of the inferior colliculus (LC) is a region of the auditory midbrain noted for receiving both auditory and somatosensory input. Anatomical studies have established that somatosensory input primarily impinges on "modular" regions of the LC, which are characterized by high densities of GABAergic neurons, while auditory input is more prominent in the "matrix" regions that surround the modules. However, how auditory and somatosensory stimuli shape activity, both individually and when combined, in the modular and matrix regions of the LC has remained unknown.

The major obstacle to progress has been the location of the LC on the lateral edge of the inferior colliculus where it cannot be accessed in vivo using conventional imaging approaches. The authors overcame this obstacle by developing methods to implant a microprism adjacent to the LC. By redirecting light from the lateral surface of the LC to the dorsal surface of the microprism, the microprism enabled two-photon imaging of the LC via a dorsal approach in anesthetized and awake mice. Then, by crossing GAD-67-GFP mice with Thy1-jRGECO1a mice, the authors showed that they could identify LC modules in vivo using GFP fluorescence while assessing neural responses to auditory, somatosensory, and multimodal stimuli using Ca2+ imaging. Critically, the authors also validated the accuracy of the microprism technique by directly comparing results obtained with a microprism to data collected using conventional imaging of the dorsal-most LC modules, which are directly visible on the dorsal IC surface, finding good correlations between the approaches.

Through this innovative combination of techniques, the authors found that matrix neurons were more sensitive to auditory stimuli than modular neurons, modular neurons were more sensitive to somatosensory stimuli than matrix neurons, and bimodal, auditory-somatosensory stimuli were more likely to suppress activity in matrix neurons and enhance activity in modular neurons. Interestingly, despite their higher sensitivity to somatosensory stimuli than matrix neurons, modular neurons in the anesthetized prep were overall more responsive to auditory stimuli than somatosensory stimuli (albeit with a tendency to have offset responses to sounds). This suggests that modular neurons should not be thought of as primarily representing somatosensory input, but rather as being more prone to having their auditory responses modified by somatosensory input. However, this trend was different in the awake prep, where modular neurons became more responsive to somatosensory stimuli. Thus, to this reviewer, one of the most intriguing results of the present study is the extent to which neural responses in the LC changed in the awake preparation. While this is not entirely unexpected, the magnitude and stimulus specificity of the changes caused by anesthesia highlight the extent to which higher-level sensory processing is affected by anesthesia and strongly suggests that future studies of LC function should be conducted in awake animals.

Together, the results of this study expand our understanding of the functional roles of matrix and module neurons by showing that responses in LC subregions are more complicated than might have been expected based on anatomy alone. The development of the microprism technique for imaging the LC will be a boon to the field, finally enabling much-needed studies of LC function in vivo. The experiments were well-designed and well-controlled, the limitations of two-photon imaging for tracking neural activity are acknowledged, and appropriate statistical tests were used.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

- Increase font size of scale bars on figure 6.

Thank you for the suggestion. We have increased the font size of the scale bar.

Reviewer #2 (Recommendations For The Authors):

Line 505: typo: 'didtinction'

Thank you for the suggestion and we do apologize for the typo. We have fixed the word as shown in the text (line 506).

No further comments.

Reviewer #3 (Recommendations For The Authors):

Line 543: Change "contripute" to "contribute"

Thank you for the suggestion and we do apologize for the typo. We have fixed the word as shown in the text (line 544).

Author response:

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

Public Reviews:

Reviewer #2 (Public Review):

The authors indicated that the adherence of ETEC is to intestinal epithelial cells. However, it is also possible that the majority of ETEC may reside in the intestinal mucus, particularly under in vivo infection condition. The colonization of ETEC in the jejunum and colon of piglets (Fig 2C) and in the intestines of mice (Fig S2A) does not necessarily reflect the adherence of ETEC to epithelial cells. Please verify these observations with other methods, such as immunostaining. Also, while Salmonella enterica serovar Typhimurium or Listeria monocytogenes can invade organoids within 1 hour, it is unknown if ETEC invade into organoids in this study. Clarifying this will help resolve if A. muciniphila block the adherence and/or invasion of ETEC. Please also address if A. muciniphila metabolites could prevent ETEC infection in the organoid models.

In the original manuscript, the sentence “ETEC K88 adheres to intestinal epithelial cells and induces gut inflammation (Yu et al., 2018)” in line 447 is a reference cited for the purpose of connecting the previous and the following, and it is not our result. We have deleted this sentence on line 457. Previous studies have shown that ETEC enter into intestinal epithelial cells after only one hour of infection (Xiao et al., 2022; Qian et al., 2023). Whether A. muciniphila metabolites prevent ETEC infection in the organoid models is not the focus of this manuscript, it may be further explored by other members of the research group in the future.

References:

Xiao K, Yang Y, Zhang Y, Lv QQ, Huang FF, Wang D, Zhao JC, Liu YL. 2022. Long-chain PUFA ameliorate enterotoxigenic Escherichia coli-induced intestinal inflammation and cell injury by modulating pyroptosis and necroptosis signaling pathways in porcine intestinal epithelial cells. Br. J. Nutr. 128(5):835-850.

Qian MQ, Zhou XC, Xu TT, Li M, Yang ZR, Han XY. 2023. Evaluation of Potential Probiotic Properties of Limosilactobacillus fermentum Derived from Piglet Feces and Influence on the Healthy and E. coli-Challenged Porcine Intestine. Microorganisms. 11(4).

Reviewer #3 (Public Review):

Summary:

The manuscript by Ma et al. describes a multi-model (pig, mouse, organoid) investigation into how fecal transplants protect against E. coli infection. The authors identify A. muciniphila and B. fragilis as two important strains and characterize how these organisms impact the epithelium by modulating host signaling pathways, namely the Wnt pathway in lgr5 intestinal stem cells.

Strengths:

The strengths of this manuscript include the use of multiple model systems and follow up mechanistic investigations to understand how A. muciniphila and B. fragilis interacted with the host to impact epithelial physiology.

Weaknesses:

After revision, the bioinformatics section of the methods is still jumbled and may indicate issues in the pipeline. Important parameters are not included to replicate analyses. Merging the forward and reverse reads may represent a problem for denoising. Chimera detection was performed prior to denoising.

Potential denoising issues for NovaSeq data was not addressed in the response. The authors did not clarify if multiple testing correction was applied; however, it may be assumed not as written. The raw sequencing data made available through the SRA accession (if for the correct project) indicates it was a MiSeq platform; however, the sample names do not appear to link up to this experimental design and metadata not sufficient to replicate analyses.

We have redescribed the method for microbiome sequencing analysis on lines 298-327.

Recommendations for the authors:

Reviewer #3 (Recommendations For The Authors):

SRA accession must be confirmed and metadata made available.

We updated the SRA data.

Author response:

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

Reviewer #1 (Recommendations For The Authors):

(1) In the first paragraph of the result section it is not clear why the authors introduce the function of p53ΔAS/ΔAS in thymocyte and then they mention fibroblasts. The authors should clarify this point. The authors should also explain based on what rationale they use doxorubicin and nutlin to analyze p53 activity (Figure 1 and figure S1). 

We thank the reviewer for this comment. In the revised manuscript, we corrected this by mentioning, at the beginning of the Results section: “We analyzed cellular stress responses in thymocytes, known to undergo a p53-dependent apoptosis upon irradiation (Lowe et al., 1993), and in primary fibroblasts, known to undergo a p53-dependent cell cycle arrest in response to various stresses - e.g. DNA damage caused by irradiation or doxorubicin (Kastan et al., 1992), and the Nutlin-mediated inhibition of Mdm2, a negative regulator of p53 (Vassilev et al., 2004).”

(2) The authors should provide quantification for the western blot in figure 2D because the reduction of p53 protein level in mutant vs wt tumors is not striking. 

In the previous version of the manuscript, the quantification of p53 bands had been included, but quantification results were mentioned below the actin bands, rather than the p53 bands, and this was probably confusing. We have corrected this in the revised version of the manuscript. The quantification results are now provided just below the p53 bands in Figs. 1B and 2D, which should clarify this point. For Figure 2D, the quantifications show a strong decrease in p53 levels for 3 out of 4 analyzed mutant tumors. For consistency purposes, in the revised manuscript the quantification results also appear below Myc bands in Fig. 2C.

(3) In the discussion section, the authors propose that a difference in Ackr4 expression may have prognostic value and that measuring ACKR4 gene expression in male patients with Burkitt lymphoma could be useful to identify the patients at higher risk. However the authors perform a lot of correlative analysis, both in mice and in patients, but the manuscript lacks of functional experiments that could help to functionally characterize Ackr4 and Mt2 in the etiology of B-cell lymphomas in males (both in mouse and in human models).

In the previous version of the manuscript, we proposed that Ackr4 might act as a suppressor of B-cell lymphomagenesis by attenuating Myc signaling. This hypothesis relied on studies showing that Ackr4 impairs the Ccr7 signaling cascade, which may lead to decreased Myc activity (Ulvmar et al., 2014; Shi et al., 2015; Bastow et al., 2021) and that the loss of Ccr7 may delay Myc-driven lymphomagenesis (Rehm et al., 2011). Furthermore, we proposed that the increased expression of Mt2 in p53ΔAS/ΔAS Em-Myc male splenic cells reflected an increase in Myc activity, because Mt2 is known to be regulated by Myc (Qin et al., 2021) and because the Mt2 promoter is bound by Myc in B cells according to experiments reported in the ChIP-Atlas database. However, in the first version of the manuscript this hypothesis might have appeared only partially supported by our data because an increase in Myc activity could be expected to have a more general impact, i.e. an impact not only on the expression of Mt2, but also on the expression of many canonical Myc target genes. In the revised manuscript, we show that this is indeed the case. We performed a gene set enrichment analysis (GSEA) comparing the RNAseq data from p53ΔAS/ΔAS Eμ-Myc and p53+/+ Eμ-Myc male splenic cells and found an enrichment of hallmark Myc targets in p53ΔAS/ΔAS Eμ-Myc cells. These new data, which strengthen our hypothesis of differences in Myc signaling intensity, are presented in Fig. 3K and Table S2.

Importantly, we now go beyond correlative analyses by providing direct experimental evidence that ACKR4 impacts on the behavior of Burkitt lymphoma cells. We used a CRISPR-Cas9 approach to knock-out ACKR4 in Raji Burkitt lymphoma cells and found that ACKR4 KO cells exhibited a 4-fold increase in chemokine-guided cell migration. These new data are presented in Figure 4F and the supplemental Figures S5-S7.  

Finally, following a suggestion of Reviewer#2, we now also point out that “Ackr4 regulates B cell differentiation (Kara et al., 2018), which raises the possibility that an altered p53-Ackr4 pathway in p53ΔAS/ΔAS Eμ-Myc male splenic cells might contribute to increase the pools of pre-B and immature B cells that may be prone to lymphomagenesis.”

In sum, we now mention in the Discussion that a decrease in Ackr4 expression might promote B-cell lymphomagenesis through three non-exclusive mechanisms.

Reviewer #2 (Recommendations For The Authors): 

(1) A great addition would be to demonstrate how p53AS specifically contributes to the regulation of Ackr4. In particular, is there evidence that p53AS might be preferentially recruited on p53 RE within that gene as compared to WT? The availability of specific antibodies that distinguish between AS and WT p53 might help to address this (experimentally complex) question. As a note, usage of such antibodies would also strengthen Fig 1B, in which the AS isoform appears as a mere faint shadow under p53, thus making its "disappearance" in trp53ΔAS/ΔAS difficult to evaluate. 

We agree with the referee that efficient antibodies against p53-AS isoforms would have been useful. In fact, we tried a non-commercial antibody developed for that purpose, but it led to many unspecific bands in western blots and appeared not reliable. Importantly however, our luciferase assays clearly show that both p53-a and p53-AS can transactivate Ackr4, a result that might be expected because these isoforms share the same DNA binding domain. Furthermore, because p53-a isoforms appear more abundant than p53-AS isoforms at the protein and RNA levels (Figs. 1B and S1A), and because the loss of p53-AS isoforms leads to a significant decrease in p53-a protein levels (Figs. 1B and 2D), we think that in p53ΔAS/ΔAS cells the reduction in p53-a levels might be the main reason for a decreased transactivation of Ackr4. This is now more clearly discussed in the revised manuscript.

(2) A most interesting observation is in Fig3 A and Fig S3, showing that spleen cells of p53ΔAS Eμ-Myc males (but not females) were enriched in pre-B and immature B cells as compared to WT counterparts. This observation points to a possible defect in B cell maturation process. It would be most interesting to determine whether this particular defect is directly mediated by a p53AS-Ackr4 axis. The hypothesis raised by the authors in the Discussion section is that increased Ackr4 expression may delay lymphomatogenesis, but data in Fig 3A and 3S actually suggest that ΔAS increases the pool of immature B-cell that may be prone to lymphomagenesis. 

We thank the reviewer for this useful comment, which we integrated in the Discussion of the revised manuscript. Ackr4 was shown to regulate B cell differentiation (Kara at al. (2018) J Exp Med 215, 801–813), so this is indeed one of the possible mechanisms by which a deregulation of the p53-Ackr4 axis might promote lymphomagenesis. We now mention: “Ackr4 regulates B cell differentiation (Kara et al., 2018), which raises the possibility that an altered p53-Ackr4 pathway in p53ΔAS/ΔAS Eμ-Myc male splenic cells might contribute to increase the pools of pre-B and immature B cells that may be prone to lymphomagenesis.” This is presented as one of three possible mechanisms by which decreased Ackr4 levels may promote tumorigenesis, the two others being the impact of Ackr4 on the chemokine-guided migration of lymphoma cells and its apparent effect on Myc signalling.

(3) The concordance with a male-specific prognostic effect of Ackr4 is most interesting in itself but is only of correlative evidence with respect to the study. Is there any information on whether p53AS expression is also a prognostic factor in BL? And is there evidence that Ackr4 may also be a male-specific prognostic factor in other B-cell malignancies, e.g. Multiple Myeloma?

We have now performed the CRISPR-mediated knock-out of ACKR4 in Burkitt lymphoma cells and found that it leads to a dramatic increase in chemokine-guided cell migration, which goes beyond correlation. This significant new result is mentioned in the revised abstract and presented in detail in Figures 4F and S5-S7.

Regarding p53-AS isoforms, they are murine-specific isoforms (Marcel et al. (2011) Cell Death Diff 18, 1815-1824), so there is no information on p53-AS expression in Burkitt lymphoma. Human p53 isoforms with alternative C-terminal domains are p53b and p53g isoforms, but the datasets we analyzed did not provide any information on the relative levels of p53a (the canonical isoform), p53b or p53g isoforms. We agree with the referee that this is an interesting question, but that cannot be answered with currently available datasets.

Regarding the different types of B-cell malignancies, we had already shown that Ackr4 is a male-specific prognostic factor in Burkitt lymphomas but not in Diffuse Large B cell lymphomas, which indicated that it is not a prognostic factor in all types of B cell lymphomas. For this revision, we also searched for its potential prognostic value in multiple myeloma, and found that, as for DLBCL, it is not a prognostic factor in this cancer type. This new analysis is presented in Figure S4C.

Author response:

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

Reviewer #1 (Public Review): 

Summary: This article explores the role of Ecdysone in regulating female sexual receptivity in Drosophila. The researchers found that PTTH, throughout its role as a positive regulator of ecdysone production, negatively affects the receptivity of adult virgin females. Indeed, loss of larval PTTH before metamorphosis significantly increases female receptivity right after adult eclosion and also later. However, during metamorphic neurodevelopment, Ecdysone, primarily through its receptor EcR-A, is required to properly develop the P1 neurons since its silencing led to morphological changes associated with a reduction in adult female receptivity. Nonetheless, the result shown in this manuscript sheds light on how Ecdysone plays a dual role in female adult receptivity, inhibiting it during larval development and enhancing it during metamorphic development. Unfortunately, this dual and opposite effect in two temporally different developmental stages has not been highlighted or explained. 

Strengths: This paper exhibits multiple strengths in its approach, employing a well-structured experimental methodology that combines genetic manipulations, behavioral assays, and molecular analysis to explore the impact of Ecdysone on regulating virgin female receptivity in Drosophila. The study provides clear and substantial findings, highlighting that removing PTTH, a positive Ecdysone regulator, increases virgin female receptivity. Additionally, the research expands into the temporal necessity of PTTH and Ecdysone function during development. 

Weaknesses: 

There are two important caveats with the data that are reflecting a weakness: 

(1) Contradictory Effects of Ecdysone and PTTH: One notable weakness in the data is the contrasting effects observed between Ecdysone and its positive regulator PTTH. PTTH loss of function increases female receptivity, while ecdysone loss of function reduces it. Given that PTTH positively regulates Ecdysone, one would expect that the loss of function of both would result in a similar phenotype or at least a consistent directional change. 

A1. As newly formed prepupae, the ptth-Gal4>UAS-Grim flies display similar changes in gene expression to the genetic control flies to response to a high-titer ecdysone pulse. These include the repression of EcR (McBrayer et al.,2007). We tested whether there is a similar feedforward relationship between PTTH and EcR-A. We quantified the EcR-A mRNA level of PTTH -/- and PTTH -/+ in the whole body of newly formed prepupae. Indeed, PTTH -/- induced increased EcR-A expression in the whole body of newly formed prepupae compared with PTTH -/+ flies. Because of the function of EcR-A in gene expression, this suggests that PTTH -/- disturbs the regulation of a serious of gene expressions during metamorphosis. However, it is not sure that the EcR-A expression in pC1 neurons is increased compared with genetic controls when PTTH is deleted. Furthermore, PTTH -/- must affect development of other neurons rather than only pC1 neurons. So, the feedforward relationship between PTTH and EcRA at the start of prepupal stage is one possible cause for the contradictory effects of PTTH -/- and EcR-A RNAi in pC1 neurons.  

(2) Discordant Temporal Requirements for Ecdysone and PTTH: Another weakness lies in the different temporal requirements for Ecdysone and PTTH. The data from the manuscript suggest that PTTH is necessary during the larval stage, as shown in Figure 2 E-G, while Ecdysone is required during the pupal stage, as indicated in Figure 5 I-K. Ecdysone is a crucial developmental hormone with precisely regulated expression throughout development, exhibiting several peaks during both larval and pupal stages. PTTH is known to regulate Ecdysone during the larval stage, specifically by stimulating the kinetics of Ecdysone peaking at the wandering stage. However, it remains unclear whether pupal PTTH, expressed at higher levels during metamorphosis, can stimulate Ecdysone production during the pupal stage. Additionally, given the transient nature of the Ecdysone peak produced at wandering time, which disappears shortly before the end of the prepupal stage, it is challenging to infer that larval PTTH will regulate Ecdysone production during the pupal stage based on the current state of knowledge in the neuroendocrine field.  

Considering these two caveats, the results suggest that the authors are witnessing distinct temporal and directional effects of Ecdysone on virgin female receptivity.  

A2. First of all, it is necessary to clarify the detailed time for the manipulation of Ptth gene and PTTH neurons. In Figure 3, activation of PTTH neurons during the stage 2 inhibited the female receptivity. The “stage 2” is from six hours before the 3rd-instar larvae to the end of the wandering larvae (the start of prepupae). In Figure 5, The “pupal stage” is from the prepupal stage to the end of pupal stage. This “pupal stage” includes the forming of prepupae when the ecdysone peak is not disappeared. The time of manipulating Ptth and EcR-A in pC1 neurons are continuous. In addition, the pC1-Gal4 expressing neurons appear also at the start of prepupal stage. So, it is possible that PTTH regulates female receptivity through the function of EcR-A in pC1 neurons. 

Reviewer #1 (Recommendations For The Authors): 

In light of the significant caveat previously discussed, I will just make a few general suggestions: 

(1) The paper primarily focuses on robust phenotypes, particularly in PTTH mutants, with a well-detailed execution of several experiments, resulting in thorough and robust outcomes. However, due to the caveat previously presented (opposite effect in larva and pupa), consider splitting the paper into two parts: Figures 1 to 4 deal with the negative effect of PTTH-Ecdysone on early virgin female receptivity, while Figures 5 to 7 focus on the positive metamorphic effect of Ecdysone in P1 metamorphic neurodevelopment. However, in this scenario, the mechanism by which PTTH loss of function increases female receptivity should be addressed.

A3. It is a good suggestion that splitting the paper into two parts associated with the PTTH function and EcR function in pC1 neurons separately, if it is impossible that PTTH functions in female receptivity through the function of EcR-A in pC1 neurons. However, because of the feedforward relationship between PTTH and EcR-A in the newly formed prepupae, and the time of manipulating Ptth and EcR-A in pC1 neurons is continuous, it is possible that these two functions are not independent of each other. So, we still keep the initial edition.

(2) Validate the PTTH mutants by examining homozygous mutant phenotypes and the dose-dependent heterozygous mutant phenotype using existing PTTH mutants. This could also be achieved using RNAi techniques.

A4. We did not get other existing PTTH mutants. We instead decreased the PTTH expression in PTTH neurons and dsx+ neurons, but did not detect the similar phenotype to that of PTTH -/-. Similarly, the overexpression through PTTH-Gal4>UAS-PTTH is also not sufficient to change female receptivity. It is possible that both decreasing and increasing PTTH expression are not sufficient to change female receptivity.

(3) Clarify if elav-Gal4 is not expressed in PTTH neurons and discuss how the rescue mechanisms work (hormonal, paracrine, etc.) in the text.

A5. We tested the overlap of elav-Gal4>GFP signal and the stained PTTH with PTTH antibody. We did not detect the overlap. It suggests that elav-Gal4 is not expressed in PTTH neurons. However, we detected the expression of PTTH (PTTH antibody) in CNS when overexpressed PTTH using elav-Gal4>UASPTTH based on PTTH -/-. Furthermore, this rescued the phenotype of PTTH -/- in female receptivity. Insect PTTH isoforms have similar probable signal peptide for secreting. Indeed, except for the projection of axons to PG gland, PTTH also carries endocrine function acting on its receptor Torso in light sensors to regulate light avoidance of larvae. The overexpressed PTTH in other neurons through elav-Gal4>UASPTTH may act on the PG gland through endocrine function and then induce the ecdysone synthesis and release. So that, although elav-Gal4 is not expressed in PTTH neurons, the ecdysone synthesis triggered by PTTH from the hemolymph may result in the rescued PTTH -/- phenotype in female receptivity.

(4) Consider renaming the new PTTH mutant to avoid confusion with the existing PTTHDelta allele. 

A6. We have renamed our new PTTH mutant as PtthDelete.

(5) Include the age of virgin females in each figure legend, especially for Figures 2 to 7, to aid in interpretation. This is essential information since wild-type early virgins -day 1- show no receptivity. In contrast, they reach a typical 80% receptivity later, and the mechanism regulating the first face might differ from the one occurring later.

A7. We have included the age of virgin females in each figure legend. 

(6) Explain the relevance of observing that PTTH adult neurons are dsx-positive, as it's unclear why this observation is significant, considering that these neurons are not responsible for the observed receptivity effect in virgin females. Alternatively, address this in the context of the third instar larva or clarify its relevance.  

A8. We decreased the DsxF expression in PTTH neurons and did not detect significantly changed female receptivity. Almost all neurons regulating female receptivity, including pC1 neurons, express DsxF. We suppose that PTTH neurons have some relationship with other DsxF-positive neurons which regulate female receptivity. Indeed, we detected the overlap of dsx-LexA>LexAop-RFP and torso-Gal4>UAS-GFP during larval stage. Furthermore, decreasing Torso expression in pC1 neurons significantly inhibit female receptivity. 

These results suggest that, PTTH regulates female receptivity not only through ecdysone, but also may through regulating other neurons especially DsxF-positive neurons associated with female receptivity directly. 

Reviewer #2 (Public Review): 

Summary: The authors tried to identify novel adult functions of the classical Drosophila juvenile-adult transition axis (i.e. ptth-ecdysone). Surprisingly, larval ptth-expressing neurons expressed the sex-specific doublesex gene, thus belonging to the sexual dimorphic circuit. Lack of ptth during late larval development caused enhanced female sexual receptivity, an effect rescued by supplying ecdysone in the food. Among many other cellular players, pC1 neurons control receptivity by encoding the mating status of females. Interestingly, during metamorphosis, a subtype of pC1 neurons required Ecdysone Receptor A in order to regulate such female receptivity. A transcriptomic analysis using pC1-specific Ecdyone signaling down-regulation gives some hints of possible downstream mechanisms. 

Strengths: the manuscript showed solid genetic evidence that lack of ptth during development caused enhanced copulation rate in female flies, which includes ptth mutant rescue experiments by overexpressing ptth as well as by adding ecdysone-supplemented food. They also present elegant data dissecting the temporal requirements of ptth-expressing neurons by shifting animals from non-permissive to permissive temperatures, in order to inactivate neuronal function (although not exclusively ptth function). By combining different drivers together with a EcR-A RNAi line authors also identified the Ecdysone receptor requirements of a particular subtype of pC1 neurons during metamorphosis. Convincing live calcium imaging showed no apparent effect of EcR-A in neural activity, although some effect on morphology is uncovered. Finally, bulk RNAseq shows differential gene expression after EcR-A down-regulation. 

Weaknesses: the paper has three main weaknesses. The first one refers to temporal requirements of ptth and ecdysone signaling. Whereas ptth is necessary during larval development, the ecdysone effect appears during pupal development. ptth induces ecdysone synthesis during larval development but there is no published evidence about a similar role for ptth during pupal stages. Furthermore, larval and pupal ecdysone functions are different (triggering metamorphosis vs tissue remodeling). The second caveat is the fact that ptth and ecdysone loss-of-function experiments render opposite effects (enhancing and decreasing copulation rates, respectively). The most plausible explanation is that both functions are independent of each other, also suggested by differential temporal requirements. Finally, in order to identify the effect in the transcriptional response of down-regulating EcR-A in a very small population of neurons, a scRNAseq study should have been performed instead of bulk RNAseq. 

In summary, despite the authors providing convincing evidence that ptth and ecdysone signaling pathways are involved in female receptivity, the main claim that ptth regulates this process through ecdysone is not supported by results. More likely, they'd rather be independent processes. 

B1. Clarification: in Figure 3, activation of PTTH neurons during the stage 2 inhibited the female receptivity. The “stage 2” is from six hours before the 3rd-instar larvae to the end of the wandering larvae (the start of prepupae). In Figure 5, The “pupal stage” is from the start of prepupal stage to the end of pupal stage. This “pupal stage” includes the forming of prepupae when the ecdysone peak is not disappeared. The time of manipulating Ptth and EcR-A in pC1 neurons are continuous. In addition, the pC1-Gal4 expressing neurons appear also at the start of prepupal stage. So, it is possible that PTTH regulates female receptivity through the function of EcR-A in pC1 neurons. 

B2. During the forming of prepupae, the ptth-Gal4>UAS-Grim flies display similar changes in gene expression to the genetic control flies to response to a high-titer ecdysone pulse. These include the repression of EcR (McBrayer et al.,2007). We tested whether there is a similar feedforward relationship between PTTH and EcR-A. We quantified the EcR-A mRNA level of PTTH -/- and PTTH -/+ in the whole body of newly formed prepupae. Indeed, PTTH -/- induced increased EcR-A compared with PTTH -/+ flies. Because of the function of EcR-A in gene expression, this suggests that PTTH -/- disturbs the regulation of a serious of gene expressions during metamorphosis. However, it is not sure that the EcR-A expression in pC1 neurons is increased compared with genetic controls when PTTH is deleted. Furthermore, PTTH -/- must affect the development of other neurons rather than only pC1 neurons. So, the feedforward relationship between PTTH and EcR-A at the start of prepupal stage is one possible cause for the contradictory effects of PTTH -/- and EcR-A RNAi in pC1 neurons.

B3. We will do single cell sequencing in pC1 neurons for the exploration of detailed molecular mechanism of female receptivity in the future.

Reviewer #2 (Recommendations For The Authors): 

Additional experiments and suggestions: 

- torso LOF in the PG to determine whether or not the ecdysone peak regulated by ptth (there is a 1-day delay in pupation) is responsible for the ptth effect in L3. In the same line, what happens if torso is downregulated in the pC1 neurons? Is there any effect on copulation rates? 

B4. Because the loss of phm-Gal4, we could not test female receptivity when decreasing the expression of Torso in PG gland. However, decreasing Torso expression in pC1 neurons significantly inhibit female receptivity. This suggests that PTTH regulates female receptivity not only through ecdysone but also through regulating dsx+ pC1 neurons in female receptivity directly.

- What is the effect of down-regulating ptth in the dsx+ neurons? No ptth RNAi experiments are shown in the paper. 

B5. We decreased PTTH expression in dsx+ neurons but did not detect the change in female receptivity.  We also decreased PTTH expression in PTTH neurons using PTTH-Gal4, also did not detect the change in female receptivity. Similarly, the overexpression through PTTH-Gal4>UAS-PTTH is also not sufficient to change female receptivity. It is possible that both decreasing and increasing PTTH expression are not sufficient to change female receptivity.

- Why are most copulation rate experiments performed between 4-6 days after eclosion? ptth LOF effect only lasts until day 3 after eclosion (but very weak-fig 1). Again, this supports the idea that ptth and ecdysone effects are unrelated.

B6. Most behavioral experiments were performed between 4-6 days after eclosion as most other studies in flies, because the female receptivity reaches the peak at that time. Ptth LOF made female receptivity enhanced from the first day after eclosion. This seems like the precocious puberty. Wild type females reach high receptivity at 2 days after eclosion (about 75% within 10 min). We suppose that Ptth LOF effect only lasts until day 3 after eclosion because too high level of receptivity of control flies to exceed.

It is not sure whether the effect of PTTH-/- in female receptivity disappears after the 3rd day of adult flies. So that it is not sure whether PTTH and EcR-A effects in pC1 neurons are unrelated.

- The fact that pC1d neuronal morphology changes (and not pC1b) does not explain the effect of EcR-A LOF. Despite it is highlighted in the discussion, data do not support the hypothesis. How do these pC1 neurons look like in a ptth mutant animal regarding Calcium imaging and/or morphology? 

B7. We detected the pattern of pC1 neurons when PTTH is deleted. Consistent with the feedforward relationship between PTTH and expression of EcR-A in newly formed prepupae, PTTH deletion induced less established pC1-d neurons contrary to that induced by EcR-A reduction in pC1 neurons. However, it is not sure that the expression of EcR-A in pC1 neurons is increased when PTTH is deleted. Furthermore, on the one hand, manipulation of PTTH has general effect on the neurodevelopment not only regulating pC1 neurons. On the other hand, the detailed pattern of pC1-b neurons which is the key subtype regulating female receptivity when EcR-A is decreased in pC1 neurons or PTTH is deleted could not be seen clearly. So, the abnormal development of pC1-b neurons, if this is true, is just one of the possible reasons for the effect of PTTH deletion on female receptivity.

- The discussion is incomplete, especially the link between ptth and ecdysone; discuss why the phenotype is the opposite (ptth as a negative regulator of ecdysone in the pupa, for instance); the difference in size due to ptth LOF might be related to differential copulation rates.  

B8. We have revised the discussion. We could not exclude the effect of size of body on female receptivity when PTTH was deleted or PTTH neurons were manipulated, although there was not enough evidence for the effect of body size on female receptivity.

- scheme of pC neurons may help. 

B9. We have tried to label pC1 neurons with GFP and sort pC1 neurons through flow cytometry sorting, but could not success. This may because the number of pC1 neurons is too low in one brain. We will try single-cell sequencing in the future. 

- Immunofluorescence images are too small.

B10. We have resized the small images.

Reviewer #3 (Public Review): 

Summary: 

This manuscript shows that mutations that disable the gene encoding the PTTH gene cause an increase in female receptivity (they mate more quickly), a phenotype that can be reversed by feeding these mutants the molting hormone, 20-hydoxyecdysone (20E). The use of an inducible system reveals that inhibition or activation of PTTH neurons during the larval stages increases and decreases female receptivity, respectively, suggesting that PTTH is required during the larval stages to affect the receptivity of the (adult) female fly. Showing that these neurons express the sex-determining gene dsx leads the authors to show that interfering with 20E actions in pC1 neurons, which are dsx-positive neurons known to regulate female receptivity, reduces female receptivity and increases the arborization pattern of pC1 neurons. The work concludes by showing that targeted knockdown of EcRA in pC1 neurons causes 527 genes to be differentially expressed in the brains of female flies, of which 123 passed a false discovery rate cutoff of 0.01; interestingly, the gene showing the greatest down-regulation was the gene encoding dopamine beta-monooxygenase. 

Strengths 

This is an interesting piece of work, which may shed light on the basis for the observation noted previously that flies lacking PTTH neurons show reproductive defects ("... females show reduced fecundity"; McBrayer, 2007; DOI 10.1016/j.devcel.2007.11.003). 

Weaknesses: 

There are some results whose interpretation seem ambiguous and findings whose causal relationship is implied but not demonstrated. 

(1) At some level, the findings reported here are not at all surprising. Since 20E regulates the profound changes that occur in the central nervous system (CNS) during metamorphosis, it is not surprising that PTTH would play a role in this process. Although animals lacking PTTH (rather paradoxically) live to adulthood, they do show greatly extended larval instars and a corresponding great delay in the 20E rise that signals the start of metamorphosis. For this reason, concluding that PTTH plays a SPECIFIC role in regulating female receptivity seems a little misleading, since the metamorphic remodeling of the entire CNS is likely altered in PTTH mutants. Since these mutants produce overall normal (albeit larger--due to their prolonged larval stages) adults, these alterations are likely to be subtle. Courtship has been reported as one defect expressed by animals lacking PTTH neurons, but this behavior may stand out because reduced fertility and increased male-male courtship (McBrayer, 2007) would be noticeable defects to researchers handling these flies. By contrast, detecting defects in other behaviors (e.g., optomotor responses, learning and memory, sleep, etc) would require closer examination. For this reason, I would ask the authors to temper their statement that PTTH is SPECIFICALLY involved in regulating female receptivity.  

C1. We agree with that, it is not surprising that PTTH regulates the profound changes that occur in the CNS during metamorphosis through ecdysone. Also, the behavioral changes induced by PTTH mutants include not only female receptivity. We will temper the statement about the function of PTTH on female receptivity.

We think there are two new points in our text although more evidences are needed in the future. On the one hand, PTTH deletion and the reduction of EcR-A in pC1 neurons during metamorphosis have opposite effects on female receptivity. On the other hand, development of pC1-b neurons regulated by EcR-A during metamorphosis is important for female receptivity.

(2) The link between PTTH and the role of pC1 neurons in regulating female receptivity is not clear. Again, since 20E controls the metamorphic changes that occur in the CNS, it is not surprising that 20E would regulate the arborization of pC1 neurons. And since these neurons have been implicated in female receptivity, it would therefore be expected that altering 20E signaling in pC1 neurons would affect this phenotype. However, this does not mean that the defects in female receptivity expressed by PTTH mutants are due to defects in pC1 arborization. For this, the authors would at least have to show that PTTH mutants show the changes in pC1 arborization shown in Fig. 6. And even then the most that could be said is that the changes observed in these neurons "may contribute" to the observed behavioral changes. Indeed, the changes observed in female receptivity may be caused by PTTH/20E actions on different neurons.

C2. As newly formed prepupae, the ptth-Gal4>UAS-Grim flies display similar changes in gene expression to the genetic control flies to response to a high-titer ecdysone pulse. These include the repression of EcR (McBrayer et al., 2007). We tested whether there is a similar feedforward relationship between PTTH and EcR-A. We quantified the EcR-A mRNA level of PTTH -/- and PTTH -/+ in the whole body of newly formed prepupae. Indeed, PTTH -/- induced upregulated EcR-A in the whole body of newly formed prepupae compared with PTTH -/+ flies. We also detected the pattern of pC1 neurons when PTTH is deleted. Consistent with the feedforward relationship between PTTH and expression of EcR-A in newly formed prepupae, PTTH deletion induced less established pC1-d neurons contrary to that induced by EcR-A reduction in pC1 neurons. 

However, it is not sure that the expression of EcR-A in pC1 neurons increases compared with genetic controls when PTTH is deleted. Furthermore, on the one hand, manipulation of PTTH has general effect on the neurodevelopment. On the other hand, the detailed pattern of pC1-b neurons which is the key subtype regulating female receptivity through EcR-A function in pC1 neurons could not be seen clearly. So, the abnormal development of pC1b neurons, if this is true, is just one of the possible reasons for the effect of PTTH deletion on female receptivity.

(3) Some of the results need commenting on, or refining, or revising:  a- For some assays PTTH behaves sometimes like a recessive gene and at other times like a semidominant, and yet at others like a dominant gene. For instance, in Fig. 1D-G, PTTH[-]/+ flies behave like wildtype (D), express an intermediate phenotype (E-F), or behave like the mutant (G). This may all be correct but merits some comment.

C3. Female receptivity increases with the increase of age after eclosion, not only for wild type flies but also PTTH mutants. At the first day after eclosion (Figure 1D), maybe the loss of PTTH in PTTH[-]/+ flies is not enough for sexual precocity as in PTTH -/-. At the second day after eclosion and after (Figure 1E-G), the loss of PTTH in PTTH[-]/+ flies is sufficient to enhance female receptivity compared with wild type flies. However, After the 2nd day of adult, female receptivity of all genotype flies increases sharply. At the 3rd day of adult and after, female receptivity of PTTH -/- reaches the peak and the receptivity of PTTH[-]/+ reaches more nearly to PTTH -/- when flies get older.  

b - Some of the conclusions are overstated. i) Although Fig. 2E-G does show that silencing the PTTH neurons during the larval stages affects copulation rate (E) the strength of the conclusion is tempered by the behavior of one of the controls (tub-Gal80[ts]/+, UAS-Kir2.1/+) in panels F and G, where it behaves essentially the same as the experimental group (and quite differently from the PTTH-Gal4/+ control; blue line).(Incidentally, the corresponding copulation latency should also be shown for these data.). ii) For Fig. 5I-K, the conclusion stated is that "Knock-down of EcR-A during pupal stage significantly decreased the copulation rate." Although strictly correct, the problem is that panel J is the only one for which the behavior of the control lacking the RNAi is not the same as that of the experimental group. Thus, it could just be that when the experiment was done at the pupal stage is the only situation when the controls were both different from the experimental. Again, the results shown in J are strictly speaking correct but the statement is too definitive given the behavior of one of the controls in panels I and K. Note also that panel F shows that the UAS-RNAi control causes a massive decrease in female fertility, yet no mention is made of this fact.

C4. i) For all figures in the text, only when all the control groups were significant different from assay group, we say the assay group is significantly different. In Figure 2E-G, the control groups were both different from the assay group only at the larval stage. The difference between two control groups may due to the genetic background. We have described more detailed statistical analysis in the legend. In addition, the corresponding copulation latency has been shown. ii) For Figure 5, we have revised the conclusion in text as “when the experiment was done at the pupal stage is the only situation when the controls were both different from the experimental.” Besides, the UAS-RNAi control causes a massive decrease in female fertility in panel F has been mentioned.

Reviewer #3 (Recommendations For The Authors): 

(1) I am not sure that PTTH neurons should be referred to as "PG neurons". I am aware that this name has been used before but the PG is a gland that does not have neurons; it is not even innervated in all insects. 

C5. Agree. “PG neurons” has been changed into “PTTH neurons”.

(2) Fig. 1A warrants some explanation. One can easily imagine what it shows but a description is warranted. 

C6. Explanation has been added.

(3) When more than one genotype is compared it would be more useful to use letters to mark the genotypes that are not statistically different from each other rather than simply using asterisks. For instance, in the case of copulation latencies shown in Fig. 1E-G, which result does the comparison refer to? For example, since the comparisons are the result of ANOVAs, which comparison receives "*" in Fig. 1F? Is it PTTH[-]/+ vs PTTH[-]/PTTH[-] or vs. +/+? 

C7. Referred genotypes and conditions were marked in all figure legends.

(4) Fig. 1H: Why is copulation latency of PTTH[-]/PTTH[-]+elav-GAL4 significantly different from that of PTTH[-]/PTTH[-]? This merits a comment. Also, why was elav-GAL4 used to effect the rescue and not the PTTH-GAL4 driver? 

C8. We could not explain this phenomenon. This may due to the different genetic backgrounds between controls. We have mentioned this in figure legend.

(5) Fig. 2C, the genotype is written in a confusing order, GAL4+UAS should go together as should LexA+LexAop. 

C9. We have revised for avoiding confusion.

(6) In Fig. 2, is "larval stage" the same period that is shown in Fig. 3A? Please clarify.

C10. We have clarified this in text and legends.

(7) Fig. 6. The fact that pC1 neurons can be labeled using the pC1-ss2-Gal4 at the start of the pupal stage does not mean that this is when these neurons appear (are born), only when they start expressing this GAL4. Other types of evidence would be needed to make a statement about the birthdate of these neurons. 

C11. We have revised the description for the appearance of pC1-ss2-Gal4>GFP. The detailed birth time of pC1 neurons will be tested in future.

(8) The results shown in Fig. 7 are not pursued further and thus appear like a prelude to the next manuscript. Unless the authors have more to add regarding the role of one of the differentially expressed genes (e.g., dopamine beta-monooxygenase, which they single out) I would suggest leaving this result out. 

C12. We have leave this out.

(9) Female flies lacking PTTH neurons were reported to show lower fecundity by McBrayer et al. (2007) and should be cited. 

C13. This important study has been cited in the first manuscript. In this revision, we have cited it again when mentioning the lower fecundity of female flies lacking PTTH neurons.

(10) Line 230: when were PTTH neurons activated? Since they are dead by 10h post-eclosion it isn't clear if this experiment even makes sense. 

C14. Yes, we did this for making sure that PTTH neurons do not affect female receptivity at adult stage again.

(11) Line 338: the statements in the figures say that PTTH function is required during the larval stages, not during metamorphosis 

C15. This has been revised as “The result suggested that EcR-A in pC1 neurons plays a role in virgin female receptivity during metamorphosis. This is consistent with that PTTH regulates virgin female receptivity before the start of metamorphosis.”

(12) Did the authors notice any abnormal behavior in males? McBrayer et al. (2007) mention that males lacking PTTH neurons show male-male courtship. This may remit to the impact of 20E on other dsx[+] neurons. 

C16. Yes, we have noticed that males lacking PTTH show male-male courtship. It is possible that PTTH deletion induces male-male courtship through the impact of 20E on other dsx+ or fru+ neurons. We have added the corresponding discussion.

(13) Line 145: please define CCT at first use 

C17. CCT has been defined.

(14) Overall the manuscript is well written; however, it would still benefit from editing by a native English speaker. I have marked a few corrections that are needed, but I probably missed some. 

+ Line 77: "If female is not willing..." should say "If THE female is not willing..." 

+ Line 78 "...she may kick the legs, flick the wings," should say "...she may kick HER legs, flick HER wings," 

+ Lines 93-94 this sentence is unclear: "...while the neurons in that fru P1 promoter or dsx is expressed regulate some aspects..." 

+ Line 108 "...similar as the function of hypothalamic-pituitary-gonadal (HPG).." should say "...similar

TO the function of hypothalamic-pituitary-gonadal (HPG).." 

+ Line 152 "Due to that 20E functions through its receptor EcR.." should say ""BECAUSE 20E ACTS through its receptor EcR.." 

+ Lines 155, 354 "unnormal" is not commonly used (although it is an English word); "abnormal" is usually used instead. 

+ Line 273: "....we then asked that whether ecdysone regulates" delete "that"  + Sentences lines 306-309 need to be revised.

C18. Thank you for your suggestions. We have revised as you advise.

Author response:

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

Reviewer #1 (Public Review): 

The reviewer retained most of their comments from the previous reviewing round. In order to meet these comments and to further examine the dynamic nature of threat omission-related fMRI responses, we now re-analyzed our fMRI results using the single trial estimates. The results of these additional analyses are added below in our response to the recommendations for the authors of reviewer 1. However, we do want to reiterate that there was a factually incorrect statement concerning our design in the reviewer’s initial comments. Specifically, the reviewer wrote that “25% of shocks are omitted, regardless of whether subjects are told that the probability is 100%, 75%, 50%, 25%, or 0%.” We want to repeat that this is not what we did. 100% trials were always reinforced (100% reinforcement rate); 0% trials were never reinforced (0% reinforcement rate). For all other instructed probability levels (25%, 50%, 75%), the stimulation was delivered in 25% of the trials (25% reinforcement rate). We have elaborated on this misconception in our previous letter and have added this information more explicitly in the previous revision of the manuscript (e.g., lines 125-129; 223-224; 486-492).   

Reviewer #1 (Recommendations For The Authors): 

I do not have any further recommendations, although I believe an analysis of learning-related changes is still possible with the trial-wise estimates from unreinforced trials. The authors' response does not clarify whether they tested for interactions with run, and thus the fact that there are main effects does not preclude learning. I kept my original comments regarding limitations, with the exception of the suggestion to modify the title. 

We thank the reviewer for this recommendation. In line with their suggestion, we have now reanalyzed our main ROI results using the trial-by-trial estimates we obtained from the firstlevel omission>baseline contrasts. Specifically, we extracted beta-estimates from each ROI and entered them into the same Probability x Intensity x Run LMM we used for the relief and SCR analyses. Results from these analyses (in the full sample) were similar to our main results. For the VTA/SN model, we found main effects of Probability (F = 3.12, p = .04), and Intensity (F = 7.15, p < .001) (in the model where influential outliers were rescored to 2SD from mean). There was no main effect of Run (F = 0.92, p = .43) and no Probability x Run interaction (F = 1.24, p = .28). If the experienced contingency would have interfered with the instructions, there should have been a Probability x Run interaction (with the effect of Probability only being present in the first runs). Since we did not observe such an interaction, our results indicate that even though some learning might still have taken place, the main effect of Probability remained present throughout the task.  

There is an important side note regarding these analyses: For the first level GLM estimation, we concatenated the functional runs and accounted for baseline differences between runs by adding run-specific intercepts as regressors of no-interest. Hence, any potential main effect of run was likely modeled out at first level. This might explain why, in contrast to the rating and SCR results (see Supplemental Figure 5), we found no main effect of Run. Nevertheless, interaction effects should not be affected by including these run-specific intercepts.

Note that when we ran the single-trial analysis for the ventral putamen ROI, the effect of intensity became significant (F = 3.89, p = .02). Results neither changed for the NAc, nor the vmPFC ROIs.  

Reviewer #2 (Public Review): 

Comments on revised version: 

I want to thank the authors for their thorough and comprehensive work in revising this manuscript. I agree with the authors that learning paradigms might not be a necessity when it comes to study the PE signals, but I don't particularly agree with some of the responses in the rebuttal letter ("Furthermore, conditioning paradigms generally only include one level of aversive outcome: the electrical stimulation is either delivered or omitted."). This is of course correct description for the conditioning paradigm, but the same can be said for an instructed design: the aversive outcome was either delivered or not. That being said, adopting the instructed design itself is legitimate in my opinion. 

We thank the reviewer for this comment. We have now modified the phrasing of this argument to clarify our reasoning (see lines 102-104: “First, these only included one level of aversive outcome: the electrical stimulation was either delivered at a fixed intensity, or omitted; but the intensity of the stimulation was never experimentally manipulated within the same task.”).  

The reason why we mentioned that “the aversive outcome is either delivered or omitted” is because in most contemporary conditioning paradigms only one level of aversive US is used. In these cases, it is therefore not possible to investigate the effect of US Intensity. In our paradigm, we included multiple levels of aversive US, allowing us to assess how the level of aversiveness influences threat omission responding. It is indeed true that each level was delivered or not. However, our data clearly (and robustly across experiments, see Willems & Vervliet, 2021) demonstrate that the effects of the instructed and perceived unpleasantness of the US (as operationalized by the mean reported US unpleasantness during the task) on the reported relief and the omission fMRI responses are stronger than the effect of instructed probability.  

My main concern, which the authors spent quite some length in the rebuttal letter to address, still remains about the validity for different instructed probabilities. Although subjects were told that the trials were independent, the big difference between 75% and 25% would more than likely confuse the subjects, especially given that most of us would fall prey to the Gambler's fallacy (or the law of small numbers) to some degree. When the instruction and subjective experience collides, some form of inference or learning must have occurred, making the otherwise straightforward analysis more complex. Therefore, I believe that a more rigorous/quantitative learning modeling work can dramatically improve the validity of the results. Of course, I also realize how much extra work is needed to append the computational part but without it there is always a theoretical loophole in the current experimental design. 

We agree with the reviewer that some learning may have occurred in our task. However, we believe the most important question in relation to our study is: to what extent did this learning influence our manipulations of interest?  

In our reply to reviewer 1, we already showed that a re-analysis of the fMRI results using the trial-by-trial estimates of the omission contrasts revealed no Probability x Run interaction, suggesting that – overall – the probability effect remained stable over the course of the experiment. However, inspired by the alternative explanation that was proposed by this reviewer, we now also assessed the role of the Gambler’s fallacy in a separate set of analyses. Indeed, it is possible that participants start to expect a stimulation more after more time has passed since the last stimulation was experienced. To test this alternative hypothesis, we specified two new regressors that calculated for each trial of each participant how many trials had passed since the last stimulation (or since the beginning of the experiment) either overall (across all trials of all probability types; hence called the overall-lag regressor) or per probability level (across trials of each probability type separately; hence called the lag-per-probability regressor). For both regressors a value of 0 indicates that the previous trial was either a stimulation trial or the start of experiment, a value of 1 means that the last stimulation trial was 2 trials ago, etc.  

The results of these additional analyses are added in a supplemental note (see supplemental note 6), and referred to in the main text (see lines 231-236: “Likewise, a post-hoc trial-by-trial analysis of the omission-related fMRI activations confirmed that the Probability effect for the VTA/SN activations was stable over the course of the experiment (no Probability x Run interaction) and remained present when accounting for the Gambler’s fallacy (i.e., the possibility that participants start to expect a stimulation more when more time has passed since the last stimulation was experienced) (see supplemental note 6). Overall, these post-hoc analyses further confirm the PE-profile of omission-related VTA/SN responses”.  

Addition to supplemental material (pages 16-18)

Supplemental Note 6: The effect of Run and the Gambler’s Fallacy 

A question that was raised by the reviewers was whether omission-related responses could be influenced by dynamical learning or the Gambler’s Fallacy, which might have affected the effectiveness of the Probability manipulation.  

Inspired by this question, we exploratorily assessed the role of the Gambler’s Fallacy and the effects of Run in a separate set of analyses. Indeed, it is possible that participants start to expect a stimulation more when more time has passed since the last stimulation was experienced. To test this alternative hypothesis, we specified two new regressors that calculated for each trial of each participant how many trials had passed since the last stimulation (or since the beginning of the experiment) either overall (across all trials of all probability types; hence called the overall-lag regressor) or per probability level (across trials of each probability type separately; hence called the lag-per-probability regressor). For both regressors a value of 0 indicates that the previous trial was either a stimulation trial or the start of experiment, a value of 1 means that the last stimulation trial was 2 trials ago, etc.  

The new models including these regressors for each omission response type (i.e., omission-related activations for each ROI, relief, and omission-SCR) were specified as follows:   

(1) For the overall lag:

Omission response ~ Probability * Intensity * Run + US-unpleasantness + Overall-lag + (1|Subject).  

(2) For the lag per probability level:

Omission response ~ Probability * Intensity * Run + US-unpleasantness + Lag-perprobability : Probability + (1|Subject).  

Where US-unpleasantness scores were mean-centered across participants; “*” represents main effects and interactions, and “:” represents an interaction (without main effect). Note that we only included an interaction for the lag-per-probability model to estimate separate lag-parameters for each probability level.  

The results of these analyses are presented in the tables below. Overall, we found that adding these lag-regressors to the model did not alter our main results. That is: for the VTA/SN, relief and omission-SCR, the main effects of Probability and Intensity remained. Interestingly, the overall-lag-effect itself was significant for VTA/SN activations and omission SCR, indicating that VTA/SN activations were larger when more time had passed since the last stimulation (beta = 0.19), whereas SCR were smaller when more time had passed (beta = -0.03). This pattern is reminiscent of the Perruchet effect, namely that the explicit expectancy of a US increases over a run of non-reinforced trials (in line with the gambler’s fallacy effect) whereas the conditioned physiological response to the conditional stimulus declines (in line with an extinction effect, Perruchet, 1985; McAndrew, Jones, McLaren, & McLaren, 2012). Thus, the observed dissociation between the VTA/SN activations and omission SCR might similarly point to two distinctive processes where VTA/SN activations are more dependent on a consciously controlled process that is subjected to the gambler’s fallacy, whereas the strength of the omission SCR responses is more dependent on an automatic associative process that is subjected to extinction. Importantly, however, even though the temporal distance to the last stimulation had these opposing effects on VTA/SN activations and omission SCRs, the main effects of the probability manipulation remained significant for both outcome variables. This means that the core results of our study still hold.   

Next to the overall-lag effect, the lag-per-probability regressor was only significant for the vmPFC. A follow-up of the beta estimates of the lag-per-probability regressors for each probability level revealed that vmPFC activations increased with increasing temporal distance from the stimulation, but only for the 50% trials (beta = 0.47, t = 2.75, p < .01), and not the 25% (beta = 0.25, t = 1.49, p = .14) or the 75% trials (beta = 0.28, t = 1.62, p = .10).

Author response table 1.

F-statistics and corresponding p-values from the overall lag model

(*) F-test and p-values were based on the model where outliers were rescored to 2SD from the mean. Note that when retaining the influential outliers for this model, the p-value of the probability effect was p = .06. For all other outcome variables, rescoring the outliers did not change the results. Significant effects are indicated in bold.

Author response table 2.

Table 2 F-statistics and corresponding p-values from the lag per probability level model

(*) F-test and p-values were based on the model where outliers were rescored to 2SD from the mean. Note that when retaining the influential outliers for this model, the p-value of the Intensity x Run interaction was p = .05. For all other outcome variables, rescoring the outliers did not change the results. Significant effects are indicated in bold.

As the authors mentioned in the rebuttal letter, "selecting participants only if their anticipatory SCR monotonically increased with each increase in instructed probability 0% < 25% < 50% < 75% < 100%, N = 11 participants", only ~1/3 of the subjects actually showed strong evidence for the validity of the instructions. This further raises the question of whether the instructed design, due to the interference of false instruction and the dynamic learning among trials, is solid enough to test the hypothesis .  

We agree with the reviewer that a monotonic increase in anticipatory SCR with increasing probability instructions would provide the strongest evidence that the manipulation worked. However, it is well known that SCR is a noisy measure, and so the chances to see this monotonic increase are rather small, even if the underlying threat anticipation increases monotonically. Furthermore, between-subject variation is substantial in physiological measures, and it is not uncommon to observe, e.g., differential fear conditioning in one measure, but not in another (Lonsdorf & Merz, 2017). It is therefore not so surprising that ‘only’ 1/3 of our participants showed the perfect pattern of monotonically increasing SCR with increasing probability instructions. That being said, it is also important to note that not all participants were considered for these follow-up analyses because valid SCR data was not always available.

Specifically, N = 4 participants were identified as anticipation non-responders (i.e. participant with smaller average SCR to the clock on 100% than on 0% trials; pre-registered criterium) and were excluded from the SCR-related analyses, and N = 1 participant had missing data due to technical difficulties. This means that only 26 (and not 31) participants were considered for the post hoc analyses. Taking this information into account, this means that 21 out of 26 participants (approximately 80%) showed stronger anticipatory SCR following 75% instructions compared to 25% instructions and that  11 out of 26 participants (approximately 40%) even showed the monotonical increase in their anticipatory SCR (see supplemental figure 4). Furthermore, although anticipatory SCR gradually decreased over the course of the experiment, there was no Run x Probability interaction, indicating that the instructions remained stable throughout the task (see supplemental figure 3).  

Reviewer #2 (Recommendations For The Authors):

A more operational approach might be to break the trials into different sections along the timeline and examine how much the results might have been affected across time. I expect the manipulation checks would hold for the first one or two runs and the authors then would have good reasons to focus on the behavioral and imaging results for those runs. 

This recommendation resembles the recommendation by reviewer 1. In our reply to reviewer 1, we showed the results of a re-analysis of the fMRI data using the trial-by-trial estimates of the omission contrasts, which revealed no Probability x Run interaction, suggesting that – overall - the probability effect remained (more or less) stable over the course of the experiment.  For a more in depth discussion of the results of this additional analysis, we refer to our answer to reviewer 1.  

Reviewer #3 (Public Review): 

Comments on revised version: 

The authors were extremely responsive to the comments and provided a comprehensive rebuttal letter with a lot of detail to address the comments. The authors clarified their methodology, and rationale for their task design, which required some more explanation (at least for me) to understand. Some of the design elements were not clear to me in the original paper. 

The initial framing for their study is still in the domain of learning. The paper starts off with a description of extinction as the prime example of when threat is omitted. This could lead a reader to think the paper would speak to the role of prediction errors in extinction learning processes. But this is not their goal, as they emphasize repeatedly in their rebuttal letter. The revision also now details how using a conditioning/extinction framework doesn't suit their experimental needs. 

We thank the reviewer for pointing out this potential cause of confusion. We have now rewritten the starting paragraph of the introduction to more closely focus on prediction errors, and only discuss fear extinction as a potential paradigm that has been used to study the role of threat omission PE for fear extinction learning (see lines 40-55). We hope that these adaptations are sufficient to prevent any false expectations. However, as we have mentioned in our previous response letter, not talking about fear extinction at all would also not make sense in our opinion, since most of the knowledge we have gained about threat omission prediction errors to date is based on studies that employed these paradigms.  

Adaptation in the revised manuscript (lines 40-55):  

“We experience pleasurable relief when an expected threat stays away1. This relief indicates that the outcome we experienced (“nothing”) was better than we expected it to be (“threat”). Such a mismatch between expectation and outcome is generally regarded as the trigger for new learning, and is typically formalized as the prediction error (PE) that determines how much there can be learned in any given situation2. Over the last two decades, the PE elicited by the absence of expected threat (threat omission PE) has received increasing scientific interest, because it is thought to play a central role in learning of safety. Impaired safety learning is one of the core features of clinical anxiety4. A better understanding of how the threat omission PE is processed in the brain may therefore be key to optimizing therapeutic efforts to boost safety learning. Yet, despite its theoretical and clinical importance, research on how the threat omission PE is computed in the brain is only emerging.  

To date, the threat omission PE has mainly been studied using fear extinction paradigms that mimic safety learning by repeatedly confronting a human or animal with a threat predicting cue (conditional stimulus, CS; e.g. a tone) in the absence of a previously associated aversive event (unconditional stimulus, US; e.g., an electrical stimulation). These (primarily non-human) studies have revealed that there are striking similarities between the PE elicited by unexpected threat omission and the PE elicited by unexpected reward.”

It is reasonable to develop a new task to answer their experimental questions. By no means is there a requirement to use a conditioning/extinction paradigm to address their questions. As they say, "it is not necessary to adopt a learning paradigm to study omission responses", which I agree with.  But the authors seem to want to have it both ways: they frame their paper around how important prediction errors are to extinction processes, but then go out of their way to say how they can't test their hypotheses with a learning paradigm.

Part of their argument that they needed to develop their own task "outside of a learning context" goes as follows: 

(1) "...conditioning paradigms generally only include one level of aversive outcome: the electrical stimulation is either delivered or omitted. As a result, the magnitude-related axiom cannot be tested." 

(2) "....in conditioning tasks people generally learn fast, rendering relatively few trials on which the prediction is violated. As a result, there is generally little intra-individual variability in the PE responses" 

(3) "...because of the relatively low signal to noise ratio in fMRI measures, fear extinction studies often pool across trials to compare omission-related activity between early and late extinction, which further reduces the necessary variability to properly evaluate the probability axiom" 

These points seem to hinge on how tasks are "generally" constructed. However, there are many adaptations to learning tasks:

(1) There is no rule that conditioning can't include different levels of aversive outcomes following different cues. In fact, their own design uses multiple cues that signal different intensities and probabilities. Saying that conditioning "generally only include one level of aversive outcome" is not an explanation for why "these paradigms are not tailored" for their research purposes. There are also several conditioning studies that have used different cues to signal different outcome probabilities. This is not uncommon, and in fact is what they use in their study, only with an instruction rather than through learning through experience, per se.

(2) Conditioning/extinction doesn't have to occur fast. Just because people "generally learn fast" doesn't mean this has to be the case. Experiments can be designed to make learning more challenging or take longer (e.g., partial reinforcement). And there can be intra-individual differences in conditioning and extinction, especially if some cues have a lower probability of predicting the US than others. Again, because most conditioning tasks are usually constructed in a fairly simplistic manner doesn't negate the utility of learning paradigms to address PEaxioms.

(3) Many studies have tracked trial-by-trial BOLD signal in learning studies (e.g., using parametric modulation). Again, just because other studies "often pool across trials" is not an explanation for these paradigms being ill-suited to study prediction errors. Indeed, most computational models used in fMRI are predicated on analyzing data at the trial level. 

We thank the reviewer for these remarks. The “fear conditioning and extinction paradigms” that we were referring to in this paragraph were the ones that have been used to study threat omission PE responses in previous research (e.g., Raczka et al., 2011; Thiele et al. 2021; Lange et al. 2020; Esser et al., 2021; Papalini et al., 2021; Vervliet et al. 2017). These studies have mainly used differential/multiple-cue protocols where either one (or two) CS+  and one CS- are trained in an acquisition phase and extinguished in the next phase. Thus, in these paradigms: (1) only one level of aversive US is used; and (2) as safety learning develops over the course of extinction, there are relatively few omission trials during which “large” threat omission PEs can be observed (e.g. from the 24 CS+ trials that were used during extinction in Esser et al., the steepest decreases in expectancy – and thus the largest PE – were found in first 6 trials); and (3) there was never absolute certainty that the stimulation will no longer follow. Some of these studies have indeed estimated the threat omission PE during the extinction phase based on learning models, and have entered these estimates as parametric modulators to CS-offset regressors. This is very informative. However, the exact model that was used differed per study (e.g. Rescorla-Wagner in Raczka et al. and Thiele et al.; or a Rescorla- Wagner–Pearce- Hall hybrid model in Esser et al.). We wanted to analyze threat omission-responses without commitment to a particular learning model. Thus, in order to examine how threat omissionresponses vary as a function of probability-related expectations, a paradigm that has multiple probability levels is recommended (e.g. Rutledge et al., 2010; Ojala et al., 2022)

The reviewer rightfully pointed out that conditioning paradigms (more generally) can be tailored to fit our purposes as well. Still, when doing so, the same adaptations as we outlined above need to be considered: i.e. include different levels of US intensity; different levels of probability; and conditions with full certainty about the US (non)occurrence. In our attempt to keep the experimental design as simple and straightforward as possible, we decided to rely on instructions for this purpose, rather than to train 3 (US levels) x 5 (reinforcement levels) = 15 different CSs. It is certainly possible to train multiple CSs of varying reinforcement rates (e.g. Grings et al. 1971, Ojala et al., 2022). However, given that US-expectation on each trial would primarily depend on the individual learning processes of the participants, using a conditioning task would make it more difficult to maintain experimental control over the level of USexpectation elicited by each CS. As a result, this would likely require more extensive training, and thus prolong the study procedure considerably. Furthermore, even though previous studies have trained different CSs for different reinforcement rates, most of these studies have only used one level of US. Thus, in order to not complexify our task to much, we decided to rely on instructions rather than to train CSs for multiple US levels (in addition to multiple reinforcement rates).

We have tried to clarify our reasoning in the revised version of the manuscript (see introduction, lines 100-113):  

“The previously discussed fear conditioning and extinction studies have been invaluable for clarifying the role of the threat omission PE within a learning context. However, these studies were not tailored to create the varying intensity and probability-related conditions that are required to systematically evaluate the threat omission PE in the light of the PE axioms. First, these only included one level of aversive outcome: the electrical stimulation was either delivered or omitted; but the intensity of the stimulation was never experimentally manipulated within the same task. As a result, the magnitude-related axiom could not be tested. Second, as safety learning progressively developed over the course of extinction learning, the most informative trials to evaluate the probability axiom (i.e. the trials with the largest PE) were restricted to the first few CS+ offsets of the extinction phase, and the exact number of these informative trials likely differed across participants as a result of individually varying learning rates. This limited the experimental control and necessary variability to systematically evaluate the probability axiom. Third, because CS-US contingencies changed over the course of the task (e.g. from acquisition to extinction), there was never complete certainty about whether the US would (not) follow. This precluded a direct comparison of fully predicted outcomes. Finally, within a learning context, it remains unclear whether brain responses to the threat omission are in fact responses to the violation of expectancy itself, or whether they are the result of subsequent expectancy updating.”

Again, the authors are free to develop their own task design that they think is best suited to address their experimental questions. For instance, if they truly believe that omission-related responses should be studied independent of updating. The question I'm still left puzzling is why the paper is so strongly framed around extinction (the word appears several times in the main body of the paper), which is a learning process, and yet the authors go out of their way to say that they can only test their hypotheses outside of a learning paradigm. 

As we have mentioned before, the reason why we refer to extinction studies is because most evidence on threat omission PE to date comes from fear extinction paradigms.  

The authors did address other areas of concern, to varying extents. Some of these issues were somewhat glossed over in the rebuttal letter by noting them as limitations. For example, the issue with comparing 100% stimulation to 0% stimulation, when the shock contaminates the fMRI signal. This was noted as a limitation that should be addressed in future studies, bypassing the critical point. 

It is unclear to us what the reviewer means with “bypassing the critical point”. We argued in the manuscript that the contrast we initially specified and preregistered to study axiom 3 (fully predicted outcomes elicit equivalent activation) could not be used for this purpose, as it was confounded by the delivery of the stimulation. Because 100% trials aways included the stimulation and 0% trials never included stimulation, there was no way to disentangle activations related to full predictability from activations related to the stimulation as such.   

Reviewer #3 (Recommendations For The Authors): 

I'm not sure the new paragraph explaining why they can't use a learning task to test their hypotheses is very convincing, as I noted in my review. Again, it is not a problem to develop a new task to address their questions. They can justify why they want to use their task without describing (incorrectly in my opinion) that other tasks "generally" are constructed in a way that doesn't suit their needs. 

For an overview of the changes we made in response to this recommendation, we refer to our reply to the public review.   

We look forward to your reply and are happy to provide answers to any further questions or comments you may have.

Author response:

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

The manuscript lacks the conclusion section to summarize their finding. The rebuttal is too simple to state where and in which way the authors have made their revisions. In this case, please return this revision to the authors and ask them revise their contribution carefully.

We now indicate in detail the places and the way that we make revisions. Specific revisions in sentences/words are marked with blue color in the main text where necessary. A conclusion is now provided at the end of the main text (lines 264-275). Other major revisions include:

(1) We add Fig. 5 as a new figure to reconstruct ovule structure of Alasemenia and to compare three- and four-winged ovules. This is followed by Fig. 6 relating to mathematical analysis.

(2) We re-organize (sequences of some) paragraphs and revise sentences in Discussion, and then divide Discussion into three parts: “Late Devonian acupulate ovules and their functions” (lines 124-150), “Late Devonian winged ovules and evolution of ovular wings” (lines 151-179), “Mathematical analysis of wind dispersal of ovules with 1-4 wings” (lines 180-262).

(3) We move “Mathematical analysis of wind dispersal of ovules with 1-4 wings” section from the supplementary information to the main text as the third part of Discussion (lines 180-262). The original paragraph headed with Mathematical analysis in Results is now modified and inserted to “Mathematical analysis of wind dispersal of ovules with 1-4 wings” section (lines 250-256). The last paragraph in the original Supplementary information is now greatly modified and presented at the end of “Mathematical analysis of wind dispersal of ovules with 1-4 wings” section (lines 256-262).

(4) With moving “Mathematical analysis of wind dispersal of ovules with 1-4 wings” section from the supplementary information to the main text, five references are accordingly added to the list (lines 278-282, 296-300, 329-330).

(5) We change the format of citing references in the main text.

We have therefore returned your manuscript to you to allow you to make the updates necessary to address the editors comments. Please ensure that you also update your preprint with the newly revised version once complete.

Many thanks for this allowance and we now make the necessary updates to address the editors’ and reviewers’ comments. At the same time, the new version is also provided as a preprint.

Reviewer #1 (Public Review):

Summary:

Winged seeds or ovules from the Devonian are crucial to understanding the origin and early evolutionary history of wind dispersal strategy. Based on exceptionally well-preserved fossil specimens, the present manuscript documented a new fossil plant taxon (new genus and new species) from the Famennian Series of Upper Devonian in eastern China and demonstrated that three-winged seeds are more adapted to wind dispersal than one-, two- and four-winged seeds by using mathematical analysis.

Many thanks for these positive comments by the reviewer.

Strengths:

The manuscript is well organised and well presented, with superb illustrations. The methods used in the manuscript are appropriate.

Many thanks for the reviewer’s positive comments.

Weaknesses:

I would only like to suggest moving the "Mathematical analysis of wind dispersal of ovules with 1-4 wings" section from the supplementary information to the main text, leaving the supplementary figures as supplementary materials.

Ok, following the suggestion, we have moved this “Mathematical analysis of wind dispersal of ovules with 1-4 wings” section to the main text (lines 180-262). It now represents the third part of Discussion. The original paragraph headed with Mathematical analysis in Results is now modified and inserted to “Mathematical analysis of wind dispersal of ovules with 1-4 wings” section (lines 250-256). The last paragraph in the original Supplementary information is now greatly modified and presented at the end of “Mathematical analysis of wind dispersal of ovules with 1-4 wings” section (lines 256-262).

Reviewer #2 (Public Review):

Summary:

This manuscript described the second earliest known winged ovule without a capule in the Famennian of Late Devonian. Using Mathematical analysis, the authors suggest that the integuments of the earliest ovules without a cupule, as in the new taxon and Guazia, evolved functions in wind dispersal.

Yes, these include our description, mathematical analysis and suggestion.

Strengths:

The new ovule taxon's morphological part is convincing. It provides additional evidence for the earliest winged ovules, and the mathematical analysis helps to understand their function.

Many thanks for these positive comments of the reviewer.

Weaknesses:

The discussion should be enhanced to clarify the significance of this finding. What is the new advance compared with the Guazia finding? The authors can illustrate the character transformations using a simplified cladogram. The present version of the main text looks flat.

To clarify the significance of this finding, the discussion is now enhanced in the following respects. We now re-organize the contents of Discussion and divide it into three parts. These three parts are entitled “Late Devonian acupulate ovules and their functions” (lines 124-150), “Late Devonian winged ovules and evolution of ovular wings” (lines 151-179), “Mathematical analysis of wind dispersal of ovules with 1-4 wings” (lines 180-262). The third part is transformed from the original Supplementary information.

Regarding new advance (Alasemenia) compared with Guazia and illustration of the character transformations:

(1) we now provide a new figure (Fig. 5) to reconstruct ovule of Alasemenia and to compare the structure of these two ovules.

(2) in the second part of Discussion, we now say “As in Alasemenia (Fig. 5a), the integumentary wings of acupulate ovule of Guazia are broad, thin and fold inwards along the abaxial side, but their numbers are four in each ovule and their free portions usually arch centripetally (Fig. 5c; Wang et al., 2022, Figure 5).”

(3) also in the second part of Discussion, we now say “Compared to Warsteinia with short and straight wings and Guazia with long but distally inwards curving wings, Alasemenia with longer and outwards extending wings would efficiently reduce the rate of descent and be more capably moved by wind. Furthermore, the quantitative analysis in mathematics indicates that three-winged ovules such as Alasemenia are more adapted to wind dispersal than four-winged ovules including Warsteinia and Guazia (see following).”

(4) in the third part of Discussion, we now say “Significantly, the maximum windward area of each wing of Alasemenia is greater than that of Guazia and Warsteinia with four wings. All these factors suggest that Alasemenia is well adapted for anemochory.”

(5) in Conclusion, we now say “Compared to Famennian four-winged ovules of Warsteinia and Guazia, Alasemenia with three distally outwards extending wings shows advantage in anemochory.”

Recommendations for the authors:

Ok, we undertake some revisions and keep some original contents.

Reviewer #1 (Recommendations For The Authors):

I would only like to suggest moving the "Mathematical analysis of wind dispersal of ovules with 1-4 wings" section from the supplementary information to the main text, leaving the supplementary figures as supplementary materials.

Ok, following the suggestion, we now move this “Mathematical analysis of wind dispersal of ovules with 1-4 wings” section to the main text (lines 180-262). It now represents the third part of Discussion.

Reviewer #2 (Recommendations For The Authors):

(1) The mathematical part as the supplement can be incorporated into the text.

Ok, following the suggestion, we now move this “Mathematical analysis of wind dispersal of ovules with 1-4 wings” section to the main text (lines 180-262). It now represents the third part of Discussion. The original paragraph headed with Mathematical analysis in Results is now modified and inserted to “Mathematical analysis of wind dispersal of ovules with 1-4 wings” section (lines 250-256). The last paragraph in the original Supplementary information is now greatly modified and presented at the end of “Mathematical analysis of wind dispersal of ovules with 1-4 wings” section (lines 256-262).

(2) The comparisons between three- or four-winged ovules are not addressed enough.

We now add Fig. 5 as a new figure. Based on this figure and revisions, the comparisons between three- and four-winged ovules now include:

a) “Their integumentary wings illustrate diversity in number (three or four per ovule), length, folding or flattening, and being straight or curving distally. As in Alasemenia (Fig. 5a), the integumentary wings of acupulate ovule of Guazia are broad, thin and fold inwards along the abaxial side, but their numbers are four in each ovule and their free portions usually arch centripetally (Fig. 5c; Wang et al., 2022, Figure 5). In contrast to Alasemenia, Warsteinia has four integumentary wings without folding and their free portions are short and straight (Rowe, 1997, TEXT-FIG. 4).” (lines 154-160).

b) “Furthermore, the quantitative analysis in mathematics indicates that three-winged ovules such as Alasemenia are more adapted to wind dispersal than four-winged ovules including Warsteinia and Guazia (see following).” (lines 166-168).

c) “The relative wind dispersal efficiency of three-winged seeds is obviously better than that of single- and two- winged seeds, and is close to that of four-winged seeds (Fig. 6). In addition, three-winged seeds have the most stable area of windward, which also ensures the motion stability in wind dispersal. Significantly, the maximum windward area of each wing of Alasemenia is greater than that of Guazia and Warsteinia with four wings.” (lines 256-261).

d) “Compared to Famennian four-winged ovules of Warsteinia and Guazia, Alasemenia with three distally outwards extending wings shows advantage in anemochory.” (lines 272-274).

(3) The significance of this finding should be well summarized with solid evidence.

It has been summarized in Abstract (lines 19-28) and is now further summarized especially in the newly provided Conclusion (lines 264-275).

Author response:

Reviewer #1

- The entire study is based on only 2 adult animals, that were used for both the single cell dataset and the HCR. Additionally, the animals were caught from the ocean preventing information about their age or their life history. This makes the n extremely small and reduces the confidence of the conclusions. 

This statement is incorrect.  While the scRNAseq was indeed performed in two animals (n=2), the HCR-FISH was performed in 3-5 animals (depending on the probe used).  These were different animals from those used for the scRNAseq.  We are partly responsible for this confusion, since we did not state the number of animals used for the HSC-FISH in the manuscript. 

- All the fluorescent pictures present in this manuscript present red nuclei and green signals being not color-blind friendly. Additionally, many of the images lack sufficient quality to determine if the signal is real. Additional images of a control animal (not eviscerated) and of a negative control would help data interpretation. Finally, in many occasions a zoomed out image would help the reader to provide context and have a better understanding of where the signal is localized. 

Fluorescent photos will be changed to color-blind friendly colors. 

Diagrams, arrows and new photos will be included as to guide readers to the signal

or labeling in cells. In the original manuscript 6 out of 7 cluster validations included a photo of a normal, non-eviscerated control.  We will make certain that this is highlighted in the resubmission and that ALL figures with HCR-FISH labeling will include data from control animals.

- The Authors frequently report the percentage of cells with a specific feature (either labelled or expressing a certain gene or belonging to a certain cluster). This number can be misleading since that is calculated after cell dissociation and additional procedures (such as staining or sequencing and dataset cleanup) that can heavily bias the ratio between cell types. Similarly, the Authors cannot compare cell percentage between anlage and mesentery samples since that can be affected by technical aspects related to cell dissociation, tissue composition and sequencing depth. 

The Reviewer has correctly identified the limitations of using cell percentages in scRNA-seq analyses. However, these percentages do offer a general overview of the sequenced cell populations and highlight potential differences between samples. In addition, these percentages, as addressed by the Reviewer, not only emphasize the shortcommings of the dissociation methods but at the same time provide some explanation for the absence of particular cell populations, as we describe in the manuscript. In our future resubmission, we will acknowledge these limitations and inform readers of any potential biases introduced by relying on these numbers.

- The Authors decided to validate only a few clusters and in many cases there are no positive controls (such as specific localization, specific function, changes between control and regenerating animals, co-stain) that could actually validate the cluster identity and the specificity of the selected marker. There is no validation of the trajectory analysis and there is no validation of the proliferating cluster with H3P or BrdU stainings. 

We validated the seven clusters that were important to reach our conclusions. Six of these had controls of normal (uneviscerated) intestine.  Nonetheless we will increase the number of cluster validations and include the dividing cell cluster using BrdU.

- It is not clear what is already known about holothurian intestine regeneration and what are the new findings in this manuscript. The Authors reference several papers throughout the whole result sectioning mentioning how the steps of regeneration, the proliferating cells, some of the markers and some of the cell composition of mesenteries and anlages was already known. 

The manuscript presents several novel findings on holothurian intestine regeneration, including:

- The integration of multiple cellular processes, reported for the first time within a single species, along with the identification of the specific mRNAs expressed by each involved cell population.

- A comparative analysis of the sea cucumber anlage structure, highlighting its similarities to previously described blastemal structures.

- The identification of the potential dedifferentiated cell populations that form the foundation of the anlage, serving as the epicenter for proliferating and differentiating cells.

We will ensure that these and other significant findings are prominently emphasized in the resubmitted manuscript.

Reviewer #2

- The spatial context of the RNA localization images is not well represented, making it difficult to understand how the schematic model was generated from the data. In addition, multiple strong statements in the conclusion should be better justified and connected to the data provided.

As explained above we will make an effort to provide a better understanding of the cellular/tissue localization of the labeled cells. Similarly, we will revise the conclusions so that the statements made are well justified.

Reviewer #3

- Possible theoretical advances regarding lineage trajectories of cells during sea cucumber gut regeneration, but the claims that can be made with this data alone are still predictive.

We are conscious that the results from these lineage trajectories are still predictive and will emphasize this in the text. Nonetheless, they are important part of our analyses that provide the theoretical basis for future experiments.

- Better microscopy is needed for many figures to be convincing. Some minor additions to the figures will help readers understand the data more clearly.

As explained above we will make an effort to provide a better

understanding of the cellular/tissue localization of the labeled cells.  Similarly, we will revise the conclusions so that the statements made are well justified.

Author response:

We sincerely appreciate the reviewers' time, effort, and thoughtful feedback, which have significantly contributed to our research.

A key concern raised was the potential overinterpretation of our data. While the reviewers acknowledged our identification of a possible synchronization mechanism among active mitral and tufted cells (MTCs) that is distance-independent, they correctly pointed out that we did not provide direct evidence showing how ensemble MTCs synchronize. We concur with their assessment and will address this in our forthcoming response to ensure a precise interpretation of our findings.

Another concern raised involves the interpretation of results obtained under Ketamine anesthesia. Since Ketamine is an NMDA receptor antagonist, which plays a crucial role in MTC-GC reciprocal synapses, this might impact our conclusions. To address this, we will include analyses demonstrating that optogenetic activation of granule cells (GCs) in an anesthetized state inhibits recorded MTCs during baseline but does not affect odor-evoked MTC firing rates. Additionally, we will thoroughly discuss the potential influence of Ketamine anesthesia on GC-MTC synapses and its implications for our findings.

Lastly, in our detailed response to the reviewers' comments, we will discuss several recent studies that are particularly relevant to our research. We will also expand on our hypothesis that parvalbumin-positive cells in the olfactory bulb may serve as key mediators of the activity- and distance-dependent lateral inhibition observed in our findings.

Author response:

We thank both reviewers for their constructive comments. We will do our best incorporating the requested analyses and answering reviewers’ questions in the revision

Author response:

General comments, factual mistakes:

Reviewer 1 - Summary: “This study builds on the observation that the kynurenine pathway is required in the conceptus, as HOO null embryos are sensitive to maternal deficiency of NAD precursors (vitamin B3) and tryptophan, and narrows the window of sensitivity to a 3-day period.”

Correction:

Vitamin B3 should not be in parentheses, because vitamin B3 and tryptophan are both NAD precursors. We also suggest that the second half of this sentence is changed to “…and narrows the window of sensitivity to a 3-day period from embryonic day 7.5 to E10.5.” Currently, it reads as if Haao-null embryos are sensitive to any 3-day period of maternal NAD precursor restriction.

Reviewer 1 – Strengths: “Abnormalities develop under conditions of maternal vitamin B3 deficiency, indicating…”

Correction:

We suggest replacing “vitamin B3 deficiency” with “NAD deficiency”, as this is more accurate.

Reviewer 2 – Strengths: “…and then re-analysis of RNA-seq datasets suggested the endoderm was the cell source of NAD synthesis.”

Correction:

We suggest re-phrasing this sentence to “…and then re-analysis of RNA-seq datasets suggested the yolk sac endoderm cells are the source of NAD de novo synthesis.”

Reviewer 1 (Public Review):

However, without analysis of embryos at later stages in this experiment it is not known how long is needed for NAD synthesis to be recovered - and therefore until when the period of exposure to insufficient NAD lasts. This information would inform the understanding of the developmental origin of the observed defects.

We are currently seeking funds to investigate the developmental origin of the observed defects. This study includes assessing how the timing of maternal NAD precursor restriction corresponds to the timing of NAD deficiency in the embryo.

More importantly, there is still a question of whether in addition to the yolk sac, there is HAAO activity within the embryo itself prior to E12.5 (when it has first been assayed in the liver - Figure 1C).

We have additional data showing that at E11.5 the embryo has no HAAO activity. We also tested E14.5 embryos with their livers removed, and these also do not have HAAO activity. We are planning to include these data sets in the revised version of this manuscript.

Reviewer 2 (Public Review):

Page 4 and Table S4. The descriptors for malformations of organs such as the kidney and vertebrae are quite vague and uninformative. More specific details are required to convey the type and range of anomalies observed as a consequence of NAD deficiency.

Kidney defects were classified as described in Cuny et al. 2020 PNAS (PMID:32015132). In brief, kidneys with a length (tip to tip) of ≤ 1.5 mm in length were counted as hypoplastic, because the average length of a normal kidney at E18.5 is 2.98 mm (2.75-3.375 mm). The one dysmorphic kidney we observed in our dataset had a cyst. We plan to include this information plus more details of the observed vertebral defects in the revised version of this manuscript.

Can the authors define whether the role of the NAD pathway in a couple of tissue or organ systems is the same? By this I mean is the molecular or cellular effect of NAD deficiency is the same in the vertebrae and organs such as the kidney. What unifies the effects on these specific tissues and organs and are all tissues and organs affected? If some are not, can the authors explain why they escape the need for the NAD pathway?

We agree that this is a very important question, but consider it beyond the scope of this manuscript. To elucidate the underlying cellular and molecular mechanisms in individual organs will require a multiomic approach because NAD is involved in hundreds of molecular and cellular processes affecting gene expression, protein levels, metabolism, etc. For details of NAD functions that have relevance to embryogenesis see Dunwoodie et al 2023 https://doi.org/10.1089/ars.2023.0349. Furthermore, organs develop at different times during embryogenesis with both distinct, but in some cases shared, molecular and cellular processes. Relating these to specific NAD functions is the challenge. We are currently seeking funds to investigate how NAD deficiency disrupts organogenesis.

Page 5 and Figure 6C. The expectation and conclusion for whether specific genes are expressed in particular cell types in scRNA-seq datasets depend on the number of cells sequenced, the technology (methodology) used, the depth of sequencing, and also the resolution of the analysis. It is therefore essential to perform secondary validation of the analysis of scRNA-seq data. At a minimum, the authors should perform in situ hybridization or immunostaining for Tdo2, Amid, Kmo, Kanu, Haao, Qprt, and Nadsyn1 or some combination thereof at multiple time points during early mouse embryogenesis to truly understand the spatiotemporal dynamics of expression and NAD synthesis.

We have tested antibodies against HAAO, KYNU, and QPRT in adult mouse liver samples (the main site of NAD de novo synthesis) which produced non-specific bands with western blotting. Therefore, in situ immunostaining  studies on embryonic tissues are not feasible. We will investigate the possibility of effectively localizing transcripts of NAD de novo synthesis enzymes using in situ hybridization.

Absolute functional proof of the yolk sac endoderm as being essential and required for NAD synthesis in the context of CNDD might require conditional deletion of Haoo in the yolk sac versus embryo using appropriate Cre driver lines or in the absence of a conditional allele, could be performed by tetraploid embryo-ES cell complementation approaches. But temporal dietary intervention can also approximate the same thing by perturbing NAD synthesis Shen the yolk sac is the primary source versus when the liver becomes the primary source in the embryo.

Reviewer 1 has a related comment. We have additional data showing that at E11.5 the embryo has no HAAO activity, like the placenta. Similarly, E14.5 embryos with their livers removed, do not have HAAO activity either. We believe this provides sufficient proof that the yolk sac endoderm is the only site of NAD de novo activity in the conceptus until the liver has formed and takes over this function.

Author response:

We are grateful to the reviewers for recognizing the importance of our work and for their helpful suggestions. We will revise our manuscript in the revised version. However, we’d like to provide provisional responses now to answer the key questions and comments from the reviewers.

(1) Both reviewers asked why we chose 24-120 hpf to measure the apoptotic rates. We chose this time window based on the following two reasons: 1) Previous studies showed that although the motor neuron death time windows vary in chick (E5-E10), mouse (E11.5-E15.5), rat (E15-E18) and human (11-25 weeks of gestation), the common feature of these time windows is that they are all the developmental periods when motor neurons contact with muscle cells. The contact between zebrafish motor neurons and muscle cells occurs before 72 hpf, which is included in our observation time window. 2) Zebrafish complete hatching during 48-72 hpf, and most organs form before 72 hpf. More importantly, zebrafish start swimming around 72 hpf, indicating that motor neurons are fully functional.

Thus, we are confident that this 24-120 hpf time window covers the time window during which motor neurons undergo programmed cell death during zebrafish early development. We frequently used “early development” in this manuscript to describe our observation. However, we missed “early” in our title. We will add “early” in the title in the revised version.

(2) Both reviewers also asked about the neurogenesis of motor neurons. Previous studies have shown that the production of spinal cord motor neurons largely ceases before 48 hpf and then the motor neurons remain largely constant until adulthood. Our observation time window covers the major motor neuron production process. Therefore, we believe that neurogenesis will not affect our data and conclusions.

(3) Both reviewers questioned the specificity of using the mnx1 promoter to label motor neurons. The mnx1 promoter has been widely used to label motor neurons in transgenic zebrafish. Previous studies have shown that most of the cells labeled in the mnx1 transgenic zebrafish are motor neurons. In this study, we observed that the neuronal cells in our sensor zebrafish formed green cell bodies inside of the spinal cord and extended to the muscle region, which is an important morphological feature of the motor neurons. Furthermore, a few of those green cell bodies turned into blue apoptotic bodies inside the spinal cord and changed to blue axons in the muscle regions at the same time, which strongly suggests that those apoptotic neurons are not interneurons. Although the mnx1 promoter might have labeled some interneurons, this will not affect our major finding that only a small portion of motor neurons died during zebrafish early development.

(4) Reviewer 2 is concerned that the estimated 50% of motor neuron death was in limb-innervating motor neurons but not in body wall-innervating motor neurons. The death of motor neurons in limb-innervating motor neurons has been extensively studied in chicks and rodents, as it is easy to undergo operations such as amputation. However, previous studies have shown this dramatic motor neuron death does not only occur in limb-innervating motor neurons but also occurs in other spinal cord motor neurons. In our manuscript, we studied the naturally occurring motor neuron death in the whole spinal cord during the early stage of zebrafish development.

(5) Reviewer 2 mentioned that we ignored the death of an identified motor neuron. Our study was to examine the overall motor neuron apoptosis rather than a specific type of motor neuron death, so we did not emphasize the death of VaP motor neurons. We agree that the dead motor neurons observed in our manuscript contain VaP motor neurons. However, there were also other types of dead motor neurons observed in our study. The reasons are as follows: 1) VaP primary motor neurons die before 36 hpf, but our study found motor neuron cells died after 36 hpf and even at 84 hpf. 2) The position of the VaP motor neuron is together with that of the CaP motor neuron, that is, at the caudal region of the motor neuron cluster. Although it’s rare, we did observe the death of motor neurons in the rostral region of the motor neuron cluster. 3) There is only one or zero VaP motor neuron in each hemisegment. Although our data showed that usually one motor neuron died in each hemisegment, we did observe that sometimes more than one motor neuron died in the motor neuron cluster. We will include this information in the revised manuscript.

(6) For the morpholinos, we did not confirm the downregulation of the target genes. These morpholino-related data are a minor part of our manuscript and shall not affect our major findings. Thus, we didn’t think we missed “important” controls. We will perform experiments to confirm the efficiency of the morpholinos or remove these morpholino-related data from the revised version.

Author Response:

We would like to thank the editors and reviewers for the careful consideration of our manuscript and their many helpful comments. We would like to provide provisional author responses to address the public reviews.

Response to Reviewer 1:

Weaknesses:

While this study convincingly describes the phenotype seen upon Drp1 loss, my major concern is that the mechanism underlying these defects in zygotes remains unclear. The authors refer to mitochondrial fragmentation as the mechanism ensuring organelle positioning and partitioning into functional daughters during the first embryonic cleavage. However, could Drp1 have a role beyond mitochondrial fission in zygotes? I raise these concerns because, as opposed to other Drp1 KO models (including those in oocytes) which lead to hyperfused/tubular mitochondria, Drp1 loss in zygotes appears to generate enlarged yet not tubular mitochondria. Lastly, while the authors discard the role of mitochondrial transport in the clustering observed, more refined experiments should be performed to reach that conclusion.

It would be difficult to answer from this study whether Drp1 has a role beyond mitochondrial fission in zygotes. However, there are several possible reasons why the Drp1 KO zygotes differs from the somatic cell Drp1 KO models.  

First, the reviewer mentions that the loss of Drp1 in oocytes leads to hyperfused/tubular mitochondria, but in fact, unlike in somatic cells, the EM images in Drp1 KO oocytes show enlarged mitochondria rather than tubular structures  (Udagawa et al. Current Biology 2014, Fig. 2C and Fig. S1B-D), as in the case of zygotes in this study. 

These mitochondrial morphologies in Drp1-deficient oocytes/zygotes may be attributed to the unique mitochondrial architecture in these cells. Mitochondria in oocytes have the shape of a small sphere with an irregular cristae located peripherally or transversely. These structural features might be the cause of insensitivity or resistance to inner membrane fusion. In addition, in our previous study (Wakai et al., Molecular Human Reproduction 2014, Fig. 2), overexpression of mitochondrial fusion factors in oocytes resulted in mitochondrial aggregation when outer membrane fusion factor Mfn1/Mfn2 was overexpressed, while overexpression of Opa1 did not cause any morphological changes. Thus, while mitochondria in oocytes/zygotes divide actively, complete fusion, including the inner membrane, as seen in somatic cells, is unlikely to occur.

As for mitochondrial transport, we do not entirely discard its role. Althogh mitochondrial intrinsic dynamics such as fission are of primary importance for the mitochondrial distribution and partitioning in embryos, the regulation of dynamics by the cytoskeletons may be important and thus needs further study, as the reviewer pointed out.

Response to Reviewer 2:

Weaknesses:

The authors first describe the redistribution of mitochondria during normal development, followed by alterations induced by Drp1 depletion. It would be useful to indicate the time post-hCG for imaging of fertilised zygotes (first paragraph of the results/Figure 1) to compare with subsequent Drp1 depletion experiments.

We will indicate the time after hCG as the reviewer pointed out. The only problem is that in this experiment, there may be a slight deviation from the actual mitochondrial distribution change (Fig. S1A) due to the manipulation time for Trim-Away (since it was performed outside of the incubator). Also, no significant delay in pronuclear formation or embryonic development was observed with Drp1 depleted zygotes.

It is noted that Drp1 protein levels were undetectable 5h post-injection, suggesting earlier times were not examined, yet in Figure 3A it would seem that aggregation has occurred within 2 hours (relative to Figure 1).

As the reviewer pointed out, the depletion of Drp1 is likely to have occurred at an earlier stage. In this study, due to the injection of various RNAs to visualize organelles such as mitochondria and chromosomes, observations were started after about 5 hours of incubation for their fluorescent proteins to be sufficiently expressed. Therefore, for the western blotting analysis, samples were taken into account their condition at the start of the observation.

Mitochondria appear to be slightly more aggregated in Drp1 fl/fl embryos than in control, though comparison with untreated controls does not appear to have been undertaken. There also appears to be some variability in mitochondrial aggregation patterns following Drp1 depletion (Figure 2-suppl 1 B) which are not discussed.

We would like to add quantitative data on mitochondrial aggregation in Drp1-depleted embryos.

The authors use western blotting to validate the depletion of Drp1, however do not quantify band intensity. It is also unclear whether pooled embryo samples were used for western blot analysis.

We would like to add the quantitative results of the intensity of the bands for the Western blot analysis. The number of embryos analyzed is described in Fig legends, from 20 (Fig. 4) to 30 (Fig. 2) pooled samples were used.

Likewise, intracellular ROS levels are examined however quantification is not provided. It is therefore unclear whether 'highly accumulated levels' are of significance or related to Drp1 depletion.

We will present to indicate quantitative results on the accumulation of ROS.

In previous work, Drp1 was found to have a role as a spindle assembly checkpoint (SAC) protein. It is therefore unclear from the experiments performed whether aggregation of mitochondria separating the pronuclei physically (or other aspects of mitochondrial function) prevents appropriate chromosome segregation or whether Drp1 is acting directly on the SAC.

It has been reported that Drp1 regulates meiotic spindle through spindle assembly checkpoint (SAC) (Zhou et al., Nature Communications 2022). We would like to mention the possibility pointed out in the discussion part.

Response to Reviewer 3:

Seemingly, there are few apparent shortcomings. Following are the specific comments to activate the further open discussion.

- Line 246: Comments on cristae morphology of mitochondria in Drp1-depleted embryos would better be added.

We would like to add a comment regarding cristae morphology.

- Regarding Figure 2H: If possible, a representative picture of Ateam would better be included in the figure. As the authors discussed in line 458, Ateam may be able to detect whether any alterations of local energy demand occurred in the Drp1-depleted embryos.

ATeam fluorescence is analyzed using a regular fluorescence microscope, not a confocal laser microscope, in order to analyze the intensity in the whole embryo (or the whole blastomere). Therefore, we are currently unable to obtain images of localized areas within the cell (e.g., around the spindle) as expected by the reviewer; as shown in the images in Figure 3-figure supplement 1C, there is a tendency to see high ATP levels at the cell periphery, but further analysis is needed for clear and definitive results.

- Line 282: In Figure 3-Video 1, mitochondria were seemingly more aggregated around female pronucleus. Is it OK to understand that there is no gender preference of pronuclei being encircled by more aggregated mitochondria?

Aggregated mitochondria are localized toward the cell center, but do not behave in such a way that they are preferentially concentrated near the female pronucleus.

- Line 317: A little more explanation of the "variability" would be fine. Does that basically mean that the Ca2+ response in both Drp1-depleted blastomeres were lower than control and blastomere with more highly aggregated mitochondria show severer phenotype compared to the other blastomere with fewer mito?

We assume that what the reviewer have pointed out is right. However, although we were able to show the bias in Ca2+ store levels between blastomeres of Drp1 depleted embryos, we did not stain mitochondria simultaneously, so we were unable to say details such as more Ca2+ stores in blastomere that inherited more mitochondria or less Ca2+ stores in blastomere with more aggregated mitochondria

- Regarding Figure 5B (& Figure 1-figure supplement 1B): Do authors think that there would be less abnormalities in the embryos if Drp1 is trim-awayed after 2-cell or 4-cell, in which mitochondria are less involved in the spindle?

The marked accumulation of mitochondria around the spindle is unique to the first cleavage and seems to be coincident with the migration of the pronuclei toward the center. Since the process of assembly of the male and female pronuclei is also an event unique to the first cleavage, abnormalities such as binucleation due to mitochondrial misplacement are thought to be a phenomenon seen only in the first cleavage. Therefore, if Drp1 is depleted at the 2-cell or 4-cell stage, chromosome segregation errors may be less frequent. However, since unequal partitioning of mitochondria is thought to occur, some abnormalities in embryonic development is likely to be observed.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

This is an interesting study investigating the mechanisms underlying membrane targeting of the NLRP3 inflammasome and reporting a key role for the palmitoylation-depalmitoylation cycle of cys130 in NRLP3. The authors identify ZDHHC3 and APT2 as the specific ZDHHC and APT/ABHD enzymes that are responsible for the s-acylation and de-acylation of NLRP3, respectively. They show that the levels of ZDHHC3 and APT2, both localized at the Golgi, control the level of palmitoylation of NLRP3. The S-acylation-mediated membrane targeting of NLRP3 cooperates with polybasic domain (PBD)-mediated PI4P-binding to target NLRP3 to the TGN under steady-state conditions and to the disassembled TGN induced by the NLRP3 activator nigericin.

However, the study has several weaknesses in its current form as outlined below.

(1) The novelty of the findings concerning cys130 palmitoylation in NLRP3 is unfortunately compromised by recent reports on the acylation of different cysteines in NLRP3 (PMID: 38092000), including palmitoylation of the very same cys130 in NLRP3 (Yu et al https://doi.org/10.1101/2023.11.07.566005), which was shown to be relevant for NLRP3 activation in cell and animal models. What remains novel and intriguing is the finding that NLRP3 activators induce an imbalance in the acylation-deacylation cycle by segregating NLRP3 in late Golgi/endosomes from de-acylating enzymes confined in the Golgi. The interesting hypothesis put forward by the authors is that the increased palmitoylation of cys130 would finally contribute to the activation of NLRP3. However, the authors should clarify the trafficking pathway of acylated-NLRP3. This pathway should, in principle, coincide with that of TGN46 which constitutively recycles from the TGN to the plasma membrane and is trapped in endosomes upon treatment with nigericin. 

We think the data presented in our manuscript are consistent with the majority of S-acylated NLRP3 remaining on the Golgi via S-acylation in both untreated and nigericin treated cells. We have performed an experiment with BrefeldinA (BFA), a fungal metabolite that disassembles the Golgi without causing dissolution of early endosomes, that further supports the conclusion that NLRP3 predominantly resides on Golgi membranes pre and post activation. Treatment of cells with BFA prevents recruitment of NLRP3 to the Golgi in untreated cells and blocks the accumulation of NLRP3 on the structures seen in the perinuclear area after nigericin treatment (see new Supplementary Figure 4A-D). We do see some overlap of NLRP3 signal with TGN46 in the perinuclear area after nigericin treatment (see new Supplementary Figure 2E), however this likely represents TGN46 at the Golgi rather than endosomes given that the NLRP3 signal in this area is BFA sensitive.  As with 2-BP and GFP-NLRP3C130S, GFP-NLRP3 spots also form in BFA / nigericin co-treated cells but not with untagged NLRP3. These spots also do not show any co-localisation with EEA1, suggesting that under these conditions, endosomes don’t appear to represent a secondary site of NLRP3 recruitment in the absence of an intact Golgi. However, we cannot completely rule out that some NLRP3 may recruited to endosomes at some point during its activation.

(2) To affect the S-acylation, the authors used 16 hrs treatment with 2-bromopalmitate (2BP). In Figure 1f, it is quite clear that NLRP3 in 2-BP treated cells completely redistributed in spots dispersed throughout the cells upon nigericin treatment. What is the Golgi like in those cells? In other words, does 2-BP alter/affect Golgi morphology? What about PI4P levels after 2-BP treatment? These are important missing pieces of data since both the localization of many proteins and the activity of one key PI4K in the Golgi (i.e. PI4KIIalpha) are regulated by palmitoylation.

We thank the reviewer for highlighting this point and agree that it is possible the observed loss of NLRP3 from the Golgi might be due to an adverse effect of 2-BP on Golgi morphology or PI4P levels. We have tested the effect of 2-BP on the Golgi markers GM130, p230 and TGN46. 2BP has marginal effects on Golgi morphology with cis, trans and TGN markers all present at similar levels to untreated control cells (Supplementary Figure 2B-D). We also tested the effect of 2-BP on PI4P levels using mCherry-P4M, a PI4P biosensor. Surprisingly, as noted by the reviewer, despite recruitment of PI4K2A being dependent on S-acylation, PI4P was still present on the Golgi after 2-BP treatment, suggesting that a reduction in Golgi PI4P levels does not underly loss of NLRP3 from the Golgi (Supplementary Figure 2A). The pool of PI4P still present on the Golgi following 2-BP treatment is likely generated by other PI4K enzymes that localise to the Golgi independently of S-acylation, such as PI4KIIIB. We have included this data in our manuscript as part of a new Supplementary Figure 2. 

(3) The authors argue that the spots observed with NLRP-GFP result from non-specific effects mediated by the addition of the GFP tag to the NLRP3 protein. However, puncta are visible upon nigericin treatment, as a hallmark of endosomal activation. How do the authors reconcile these data? Along the same lines, the NLRP3-C130S mutant behaves similarly to wt NLRP3 upon 2-BP treatment (Figure 1h). Are those NLRP3-C130S puncta positive for endosomal markers? Are they still positive for TGN46? Are they positive for PI4P?

This is a fair point given the literature showing overlap of NLRP3 puncta formed in response to nigericin with endosomal markers and the similarity of the structures we see in terms of size and distribution to endosomes after 2BP + nigericin treatment. We have tested whether these puncta overlap with EEA1, TGN46 or PI4P (Supplementary Figure 2A, E-G). The vast majority of spots formed by GFP-NLRP3 co-treated with 2-BP and nigericin do not co-localise with EEA1, TGN46 or PI4P. This is consistent with these spots potentially being an artifact, although it has recently been shown that human NLRP3 unable to bind to the Golgi can still respond to nigericin (Mateo-Tórtola et al., 2023). These puncta might represent a conformational change cytosolic NLRP3 undergoes in response to stimulation, although our results suggest that this doesn’t appear to happen on endosomes.

(4) The authors expressed the minimal NLRP3 region to identify the domain required for NLRP3 Golgi localization. These experiments were performed in control cells. It might be informative to perform the same experiments upon nigericin treatment to investigate the ability of NLRP3 to recognize activating signals. It has been reported that PI4P increases on Golgi and endosomes upon NG treatment. Hence, all the differences between the domains may be lost or preserved. In parallel, also the timing of such recruitment upon nigericin treatment (early or late event) may be informative for the dynamics of the process and of the contribution of the single protein domains.

This is an interesting point which we thank the reviewer for highlighting. However, we think that each domain on its own is not capable of responding to nigericin as shown by the effect of mutations in helix115-125 or the PB region in the full-length NLRP3 protein. NLRP3HF, which still contains a functional PB region, isn’t capable of responding to nigericin in the same way as wild type NLRP3 (Supplementary Figure 6C-D). Similarly, mutations in the PB region of full length NLRP3 that leave helix115-125 intact show that helix115-125 is not sufficient to allow enhanced recruitment of NLRP3 to Golgi membranes after nigericin treatment (Supplementary Figure 9A). We speculate that helix115-125, the PB region and the LRR domain all need to be present to provide maximum affinity of NLRP3 for the Golgi prior to encounter with and S-acylation by ZDHHC3/7. Mutation or loss of any one of the PB region, helix115-125 or the LRR lowers NLRP3 membrane affinity, which is reflected by reduced levels of NLRP3 captured on the Golgi by S-acylation at steady state and in response to nigericin. 

(5) As noted above for the chemical inhibitors (1) the authors should check the impact of altering the balance between acyl transferase and de-acylases on the Golgi organization and PI4P levels. What is the effect of overexpressing PATs on Golgi functions?

We have checked the effect of APT2 overexpression on Golgi morphology and can show that it has no noticeable effect, ruling out an impact of APT on Golgi integrity as the reason for loss of NLRP3 from the Golgi in the presence of overexpressed APT2. We have included these images as Supplementary Figure 11H-J. 

It is plausible that the effects of ZDHHC3 or ZDHHC7 on enhanced recruitment of NLRP3 to the Golgi may be via an effect on PI4P levels since, as mentioned above, both enzymes are involved in recruitment of PI4K2A to the Golgi and have previously been shown to enhance levels of PI4K2A and PI4P on the Golgi when overexpressed (Kutchukian et al., 2021). However, NLRP3 mutants with most of the charge removed from the PB region, which are presumably unable to interact with PI4P or other negatively charged lipids, are still capable of being recruited to the Golgi by excess ZDHHC3. This would suggest that the effect of overexpressed ZDHHC3 on NLRP3 is largely independent of changes in PI4P levels on the Golgi and instead driven by helix115-125 and S-acylation at Cys-130. The latter point is supported by the observation that NLRP3HF and NLRP3Cys130 are insensitive to ZDHHC3 overexpression.

At the levels of HA-ZDHHC3 used in our experiments with NLRP3 (200ng pEF-Bos-HAZDHHC3 / c.a. 180,000 cells) we don’t see any adverse effect on Golgi morphology (Author response image 1), although it has been noted previously by others that higher levels of ZDHHC3 can have an impact on TGN46 (Ernst et al., 2018). ZDHHC3 overexpression surprisingly has no adverse effects on Golgi function and in fact enhances secretion from the Golgi (Ernst et al., 2018).  

Author response image 1.

Overexpression of HA-ZDHHC3 does not impact Golgi morphology. A) Representative confocal micrographs of HeLaM cells transfected with 200 ng HA-ZDHHC3 fixed and stained with antibodies to STX5 or TGN46. Scale bars = 10 µm. 

Reviewer #2 (Public Review):

Summary:

This paper examines the recruitment of the inflammasome seeding pattern recognition receptor NLRP3 to the Golgi. Previously, electrostatic interactions between the polybasic region of NLRP3 and negatively charged lipids were implicated in membrane association. The current study reports that reversible S-acylation of the conserved Cys-130 residue, in conjunction with upstream hydrophobic residues plus the polybasic region, act together to promote Golgi localization of NLRP3, although additional parts of the protein are needed for full Golgi localization. Treatment with the bacterial ionophore nigericin inhibits membrane traffic and prevents Golgi-associated thioesterases from removing the acyl chain, causing NLRP3 to become immobilized at the Golgi. This mechanism is put forth as an explanation for how NLRP3 is activated in response to nigericin.

Strengths:

The experiments are generally well presented. It seems likely that Cys-130 does indeed play a previously unappreciated role in the membrane association of NLRP3.

Weaknesses:

The interpretations about the effects of nigericin are less convincing. Specific comments follow.

(1) The experiments of Figure 4 bring into question whether Cys-130 is S-acylated. For Cys130, S-acylation was seen only upon expression of a severely truncated piece of the protein in conjunction with overexpression of ZDHHC3. How do the authors reconcile this result with the rest of the story?

Providing direct evidence of S-acylation at Cys-130 in the full-length protein proved difficult. We attempted to detect S-acylation of this residue by mass spectrometry. However, the presence of the PB region and multiple lysines / arginines directly after Cys-130 made this approach technically challenging and we were unable to convincingly detect S-acylation at Cys-130 by M/S. However, Cys-130 is clearly important for membrane recruitment as its mutation abolishes the localisation of NLRP3 to the Golgi. It is feasible that it is the hydrophobic nature of the cysteine residue itself which supports localisation to the Golgi, rather than S-acylation of Cys-130. A similar role for cysteine residues present in SNAP-25 has been reported (Greaves et al., 2009). However, the rest of our data are consistent with Cys-130 in NLRP3 being S-acylated. We also refer to another recently published study which provides additional biochemical evidence that mutation of Cys-130 impacts the overall levels of NLRP3 S-acylation (Yu et al., 2024). 

(2) Nigericin seems to cause fragmentation and vesiculation of the Golgi. That effect complicates the interpretations. For example, the FRAP experiment of Figure 5 is problematic because the authors neglected to show that the FRAP recovery kinetics of nonacylated resident Golgi proteins are unaffected by nigericin. Similarly, the colocalization analysis in Figure 6 is less than persuasive when considering that nigericin significantly alters Golgi structure and could indirectly affect colocalization. 

We agree that it is likely that the behaviour of other Golgi resident proteins are altered by nigericin. This is in line with a recent proteomics study showing that nigericin alters the amount of Golgi resident proteins associated with the Golgi (Hollingsworth et al., 2024) and other work demonstrating that changes in organelle pH can influence the membrane on / off rates of Rab GTPases (Maxson et al., 2023). However, Golgi levels of other peripheral membrane proteins

that associate with the Golgi through S-acylation, such as N-Ras, appear unaltered (Author response image 2.), indicating a degree of selectivity in the proteins affected. Our main point here is that NLRP3 is amongst those proteins whose behaviour on the Golgi is sensitive to nigericin and that this change in behaviour may be important to the NLRP3 activation process, although this requires further investigation and will form the basis of future studies. 

The reduction in co-localisation between NLRP3 and APT2, due to alterations in Golgi organisation and trafficking, was the point we were trying to make with this figure, and we apologise if this was not clear. We think that the changes in Golgi structure and function caused by nigericin potentially affect the ability of APT2 to encounter NLRP3 and de-acylate it. We have added a new paragraph to the results section to hopefully explain this more clearly. We recognise that our results supporting this hypothesis are at present limited and we have toned down the language used in the results section to reflect the nature of these findings..  

Author response image 2.

S-acylated peripheral membrane proteins show differential sensitivity to nigericin. A) Representative confocal micrographs of HeLaM cells coexpressing GFP-NRas and an untagged NLRP3 construct. Cells were left untreated or treated with 10 µM nigericin for 1 hour prior to fixation. Scale bars = 10 µm. B) Quantification of GFP-NRas or NLRP3 signal in the perinuclear region of cells treated with or without nigericin

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

(1) Does overnight 2-BP treatment potentially have indirect effects that could prevent NLRP3 recruitment? It would be useful here to show some sort of control confirming that the cells are not broadly perturbed.

Please see our response to point (2) raised by reviewer #1 which is along similar lines. 

(2) In Figure 5, "Veh" presumably is short for "Vehicle". This term should be defined in the legend.

We have now corrected this.

References

Ernst, A.M., S.A. Syed, O. Zaki, F. Bottanelli, H. Zheng, M. Hacke, Z. Xi, F. Rivera-Molina, M. Graham, A.A. Rebane, P. Bjorkholm, D. Baddeley, D. Toomre, F. Pincet, and J.E. Rothman. 2018. SPalmitoylation Sorts Membrane Cargo for Anterograde Transport in the Golgi. Dev Cell. 47:479-493 e477.

Greaves, J., G.R. Prescott, Y. Fukata, M. Fukata, C. Salaun, and L.H. Chamberlain. 2009. The hydrophobic cysteine-rich domain of SNAP25 couples with downstream residues to mediate membrane interactions and recognition by DHHC palmitoyl transferases. Mol Biol Cell. 20:1845-1854.

Hollingsworth, L.R., P. Veeraraghavan, J.A. Paulo, J.W. Harper, and I. Rauch. 2024. Spatiotemporal proteomic profiling of cellular responses to NLRP3 agonists. bioRxiv.

Kutchukian, C., O. Vivas, M. Casas, J.G. Jones, S.A. Tiscione, S. Simo, D.S. Ory, R.E. Dixon, and E.J. Dickson. 2021. NPC1 regulates the distribution of phosphatidylinositol 4-kinases at Golgi and lysosomal membranes. EMBO J. 40:e105990.

Mateo-Tórtola, M., I.V. Hochheiser, J. Grga, J.S. Mueller, M. Geyer, A.N.R. Weber, and A. TapiaAbellán. 2023. Non-decameric NLRP3 forms an MTOC-independent inflammasome. bioRxiv:2023.2007.2007.548075.

Maxson, M.E., K.K. Huynh, and S. Grinstein. 2023. Endocytosis is regulated through the pHdependent phosphorylation of Rab GTPases by Parkinson’s kinase LRRK2. bioRxiv:2023.2002.2015.528749.

Yu, T., D. Hou, J. Zhao, X. Lu, W.K. Greentree, Q. Zhao, M. Yang, D.G. Conde, M.E. Linder, and H. Lin. 2024. NLRP3 Cys126 palmitoylation by ZDHHC7 promotes inflammasome activation. Cell Rep. 43:114070.

Author response:

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

Reviewer 1:

Strengths

We thank the reviewer for recognizing the strengths of our in vivo Ca2+ measurements, super resolution microscopy and assessment of the secretory dysfunction in the Sjogrens syndrome mouse model.

Weaknesses

Point 1: The less restricted Ca2+ signal to the apical region of the acinar cell is not really relevant to the reduced activation of TMEM16a by a local signal at the apical plasma membrane.

We agree that the spatially averaged Ca2+ signal is not indicative of the local Ca2+ signal that activates TMEM16a. The description of the disordered Ca2+ signal in the disease model was intended to simply convey that the Ca2+ signal is altered in the model. Whether or indeed how the altered spatial characteristics of the signal are deleterious is not known but we speculate in the discussion that this contributes to the ultrastructural damage observed.

Point 2. Secretion is decreased but the amplitude of the globally averaged Ca2+ signals are increased. No proof is offered that the greater distance between IP3R and TMEM16a is the reason for decreased secretion in the face of this increased peak signal.

We have now added new data that indicates that the local Ca2+ signal is indeed disrupted in the disease model. We show that in control animals, activation of TMEM16a by application of agonist occurs when the pipette is buffered with the slower buffer EGTA but not with the fast buffer BAPTA In contrast, in cells isolated from DMXAA -treated animals both EGTA and BAPTA abolish the agonist-induced currents (new Figure 6). These data are consistent with our super resolution data showing the distance between IP3R and TMEM16a being greaterand thus presumably is enough to allow buffering of Ca2+ release from IP3R such that it does not effectively activate TMEM16a. These data also would suggest that the increased amplitude of the spatially averaged Ca2+ signal is not sufficient to overcome this structural change.

Point 3. Lack of evidence that the mitochondrial changes are associated with the defect in fluid secretion.

We agree that a causal link between the decreased secretion and altered mitochondrial morphology and function is not established. Nevertheless, we feel it is reasonable to contend that profound changes in mitochondrial morphology observed at the light and EM level, together with changes in mitochondrial membrane potential and oxygen consumption are consistent with contributing to altered fluid secretion given that this is an energetically costly process. We have altered the discussion to reflect these caveats and ideas.

Reviewer 2:

We thank the reviewer for their assessment of our work and constructive comments.

Reviewer 3:

We thank the reviewer for their careful appraisal of our manuscript and insightful comments. 

Point 1: Are all the effects of DMXAA mediated through the STING pathway?

This is an important point because as noted DMXAA has been reported to inhibit NAD(P)H quinone oxireductase that could contribute to the phenotype reported here. In future studies we intend to test other STING pathway agonists such as MSA-2 and perhaps antagonists of the STING pathway. We have added text to the discussion indicating that all the effects observed may not be a result of activation of the STING pathway.

Point 2: As noted, and clarified in the text, the driving force for ATP production is the electrochemical H+ gradient which establishes the mitochondrial membrane potential.

Point 3:  The reviewer suggested there was a decrease mitochondrial membrane potential in the absence of a change in TMRE steady state.

We apologize for the confusion generated from the presentation of the figure. We normalized TMRE fluorescence against Mitotraker green fluorescence but as shown, the figure does not reflect that the absolute TMRE fluorescence was indeed decreased. Supplemental figure 4 now shows the basal TMRE fluorescence.

Point 4: Indications that the disruption to ER structure seen in Electron Micrographs contributes to the changes in Ca2+ signal and fluid secretion.

We did not focus on the relative distance between ER and apical PM in the EMs primarily because the ER that projects towards the apical PM is a relatively minor component of the specialized ER expressing IP3R and is difficult to identify. We note that the disruption of the bulk ER as quantitated by altered ER-mitochondrial interfaces and fragmentation is consistent with our super resolution data and thus likely plays a role in the mechanism that results in dysregulated Ca2+ signals and reduced secretion.

Recommendations to Authors:

Reviewing Editor:

(1) The Editor suggests that we should use the activity of TMEM16a to directly measure the [Ca2+] experienced by the channel.

We now present new additional data.  First, we show an extended range of pipette [Ca2+] demonstrating identical Ca2+ sensitivity in DMXAA vs vehicle treated cells (Figure 5). Second, importantly, we now present data evaluating the ability of muscarinic stimulation to activate TMEM16a in the presence of either EGTA (slow Ca2+ buffer) or BAPTA (fast Ca2+ buffer). Notably, currents can be stimulated in control cells when the pipette is buffered with EGTA, but not in DMXAA treated cells. BAPTA inhibits activation in both situations (new Figure 6). These data are consistent with TMEM16a being activated by Ca2+ in a microdomain and that this is disrupted in the disease model.   

(2) The Editor asks whether a decrease in IP3R3 in a subset of the samples could account for the decreased fluid secretion.

We think this is unlikely given, as noted by the Editor, that a reduction only occurred in a subset of the samples and statistically there was no significant difference to vehicle-treated animals. Moreover, we would note that there is also no difference in the expression of IP3R2 between experimental groups and in studies of transgenic mice where either IP3R2 or IP3R3 were knocked out individually, there was no effect on salivary fluid secretion, indicating that expression of a single subtype can support stimulus-secretion coupling.

(3) Absolute values for changes in fluorescence (over time) should be included together with SD images.

These have been added in Figure 3.

(4) DMXAA has additional effects to STING activation and thus other STING pathway modulators should be used.

We agree that additional STING agonists should be explored in the future but believe that this is beyond the scope of the present studies. Additional text has been added to the discussion acknowledging the additional targets of DMXAA and that they could contribute to the phenotype.

(5) No causal link between the observed Ca2+ changes and mitochondrial dysfunction.

We agree that no experimental evidence is offered to directly support this contention. Nevertheless, dysregulated Ca2+ signals are well-documented to lead to altered mitochondrial structure and function and thus we feel it not unreasonable to speculate that this is a possibility.

(6) The paper would be improved by directly assessing mechanistic connections between altered Ca2+ signaling and TMEM16a activation.

We agree, please refer to point 1 and new figure 6.

Reviewer 1:

(1) Standard Deviation images should be explained and the location of ROI identified.

We contend that Standard Deviation images provide an effective visualization (in a single image) of both the magnitude of the Ca2+ increase and the degree of recruitment of cells in the field of view during the entire period of stimulation.  We have added text to describe the utility of this technique. Nevertheless, we now show kinetic traces of the changes in fluorescence over time in both apical and basal regions in Figure 3. We also clarify that the traces shown in Figure 2 are averaged over the entire cell. 

(2) The Authors should consider that reduced secretion is because cells are dying.

We believe this is unlikely given the lack of morphological changes in glandular structure and the minor lymphocyte infiltration observed in this model. Nevertheless, we now add data showing that the mass of SMG is not altered in the DMXAA-treated animals compared with vehicle-treated (Figure 1E).

(3) The role of mitochondria in the DMXAA phenotype is unclear. What is the effect of acutely de-energizing mitochondria on fluid secretion.

Since fluid secretion is an energetically expensive undertaking, it is not unreasonable to suggest that compromised mitochondrial function may impact secretion. That being said this could occur at multiple levels- production of ATP to fuel the Na/K pump to establish membrane gradients or to provide energy to sequester Ca2+ among a multitude of targets. This will be a subject of ongoing experiments. We contend that experiments to acutely disrupt salivary mitochondria in vivo while assessing fluid secretion would be difficult experiments to perform and interpret given that local administration of agents to SMG would not effect the other major salivary glands and systemic administration would be predicted to have wide-ranging off target effects. 

(4) Could a subset of cells with low IP3R numbers contribute to reduced fluid secretion?

Please see the response to Reviewing Editors point 2. 

(5) An attempt to estimate the effect of the spatial distruption of IP3R and TMEM16a localization should be made.

Please see the response to Reviewing Editors point 1.

Minor Points

We have amended the statement form “Highly expressed” to increased.

Regions of the cell have been labelled for orientation in the line scans.

The molecular weight markers have been added in Figure 4.

Reviewer 2:

(1) Whether mitochondrial dysfunction is the initiator of the phenotype or a result of the dysregulated Ca2+ signal is unclear.

We agree that our data does not clarify a classic “Chicken vs Egg” conundrum. We plan further experiments to address this issue. Future plans include repeating the mitochondrial and Ca2+ signaling experiments at earlier time points where we know fluid secretion is not yet impacted. This may potentially reveal the temporal sequence of events. Similarly, we plan experiments to mechanistically address why the global Ca2+ signal is augmented- reduced Ca2+ clearance or enhanced Ca2+ release/influx are possibilities. We speculate that reduced Ca2+ clearance, either because mitochondrial Ca2+ uptake is reduced or as a secondary consequence of reduced ATP levels on SERCA and PMCA is a likely possibility.

(2) Measurement of ECAR and direct measurements of ATP and Seahorse methods.

In a separate series of experiments, we monitored ECAR. These data were unfortunately very variable and difficult to interpret, although no obvious compensatory increase was observed. We plan in the future to directly monitor ATP levels in acinar cells using Mg-Green. To normalize for cell numbers in the Seahorse experiments, following centrifugation, cell pellets of equal volume were resuspended in equal volumes of buffer. Acinar cells were seeded onto Cell Tak coated dishes. This information is added to the Methods section.

Author response:

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

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):  

(1) When introducing the different antibody clones recognizing Pan, oxidized, or reduced forms, please clearly indicate which clone number belongs to which form.  

- We see where the original language could be confusing. Please see our new introduction to the antibodies used.

“we evaluated the redox state of La in fusing osteoclasts using recently validated monoclonal α-La antibodies that recognize oxidized La (clone 7B6) or reduced La (clone 312B), or do not distinguish between these La species (Pan, clone 5B9)”

(2) "Finding that the surface La pool, which promotes multinucleation in osteoclasts, is an oxidized species..." I would suggest rewording as "...is enriched in oxidized species".  

- Agreed. We have edited the sentence as follows.

“Finding that the surface La pool, which promotes multinucleation in osteoclasts, is enriched in an oxidized species raised the question”

(3) Although not necessary to support the conclusions of the manuscript, it would be interesting to know if the application of La194-408 to osteoclast progenitors following NAC treatment results in the rescue of La staining at the cell surface, or if this exogenous La is acting independently from cell surface association.  

- We agree that this is an interesting idea. We previously demonstrated that we could add La 1-375 to osteoclast progenitors following RANKL addition and promote osteoclast fusion. We also demonstrated that La 1-375 under these conditions enriched La surface staining (PMID: 36739273)

- Therefore, we hypothesize that La 194-408 would act similarly.

(4) Is the confirmation of La modified by the conversion of Cys 232 and 245 to alanine? What about the potential to form oligomers?  

- To directly answer the Reviewer’s question – we simply do not know and do not have a simple way to test this. To speculate, the differential recognition of La that is reduced vs oxidized by the antibodies used here (specifically clone 312b vs clone 7b6) suggests that some conformational change is taking place when redox signaling modifies La in osteoclasts. Moreover, in Supp. Fig. 4b, we show that recombinant La 194-408 does form a small amount of dimer under our conditions while La 194-408 Cys 232 and 245 to Ala does not. These data together weakly support that La, when converted from reduced to oxidized forms or when we artificially Cys 232 and 245 to Ala, undergoes some conformational and oligomeric change. However, we are not comfortable making

such claims in the manuscript currently and prefer to investigate this with more rigor and comment in the biological significance of these potential changes in the future.

(5) "In conclusion, in this study, we identified redox signaling as a molecular switch that redirects La protein away from the nucleus, where it protects precursor tRNAs from exonuclease digestion, and towards its osteoclast-specific function at the cell surface..." I would suggest rewording this sentence given that there is no evidence that the function of oxidized La at the cell surface is osteoclast-specific. This phenomenon could be applicable to other cell types and other biological processes.  

- The Reviewer makes a good point here, that we very much appreciate. We hoped to communicate that this was a unique function of La that was different from the well-recognized role this protein plays in RNA metabolism, but somewhat overstated past our intention. Please see where we have modified this statement to read:

“In conclusion, in this study, we identified redox signaling as a molecular switch that redirects La protein away from the nucleus, where it protects precursor tRNAs from exonuclease digestion, and towards its separable function at the osteoclast surface, where La regulates the multinucleation and resorptive functions of these managers of the skeleton.”

(6) In methods, the definition of TCEP is missing a closed parenthesis sign.  

- Thank you, corrected.

(7) In methods under "Cells" there is a missing superscript in 1x106 cells/ml. Presumably, this is 1x10e6.   

- Thank you, corrected.

(8) Please provide the sequences of primers used for RT-PCR in this study.  

- Understood. Please see where a table of all primer sequences used has been added to the Methods under the Transcript Analysis section.

(9) In methods, "Bone resorption" should be relabeled given that the osteoclasts are plated on calciumphosphate plates and not on a bone surface.  

- Thank you. Please see where in the Methods both the title and all references to “bone resorption” in the method description have now been changed to “mineral resorption”.

(10) In several figures, it would be more appropriate to correct for multiple comparisons in the statistical analyses.  

- We appreciate this concern. Please see where Fig. 2b,c; Fig. 3 b,c; Fig. 4d; Fig. 5b,d; and Fig. 6d have been reanalyzed using paired one-way ANOVAs corrected for multiple comparisons. Now all data where t-tests are used to evaluate statistical significance are only evaluating  differences between 2 values and all experiments considering 3+ values are compared using one-way ANOVAs corrected for multiple comparisons.

(11) Figure 5: Panels D and E are flipped relative to the legend. Please also define the reagent used for ROS signal in the legend.  

- Thank you. D and E are now corrected and we added “(Grey = CellRox Dye)” to the end of the legend for Fig. 5a.

(12) Supplemental Figure 5c: in the control condition, why are some nuclei not staining with the reduced La antibody?  

- Great question, direct answer – we simply do not know.  

Longer answer, this image is in fact representative and not exclusive to the reduced La antibody (clone 312b). When we look at La staining in mature, multinucleated osteoclast nuclei at later timepoints post fusion using even pan antibodies, we find that its localization to the nuclei of syncytial osteoclasts is not uniform, but that nuclear La preferentially enriches in some mature osteoclast nuclei and seems to be excluded from others. This may suggest that – akin to myonuclei in skeletal muscle – osteoclast nuclei in a syncytium are not all equal. However, we are far, far away from being able to make any conclusions from the data we have.

(13) Figure 7 legend: consider breaking this legend up into multiple sentences.  

- Thank you for the suggestion. The legend for Figure 7 has been rewritten.

Reviewer #2 (Recommendations For The Authors):  

(1) Can the authors use the official name of La protein in NCBI GENE and PROTEIN?  

- While some in the field refer to lupus La protein as La protein, we choose to refer to it simply as La, as is common throughout the Lupus La Protein literature. It is our opinion that continuously referring to a protein as a name + the word protein throughout the manuscript is unnecessary and alters the flow of our manuscript’s points.

Thanks. We have included the official name of human La in NCBI GENE ((SSB small RNA binding exonuclease protection factor La, Gene ID 6741, NCBI GENE)  into the revised text.  

(2) The references 26 and 27 are not representative. The pioneering work from Mundy, Chambers, and Almeida (PBMID 2312718, 15528306, and 24781012) should be cited.  

- Thanks. We have added these 3 references to better acknowledge these significant contributions.

(3) It is hard to understand Figure 2. What are the white arrows in Figure 2a pointed to? In Figure 2b, what do the columns a-LA(Red), a-La (Pan), and a-La (Ox) mean, treatment, or staining? Figure 2c, the legend "conditions where surface proteins are oxidized (TCEP) seems to be "deoxidized.  

- We agree. We now realized this legend was rather confusing. It has been edited to read

“(a) Representative fluorescence and DIC confocal micrographs of primary human osteoclasts following synchronized cell-cell fusion where hemifusion inhibitor was left (Inhibition), removed (Wash) or removed but the α-La antibodies indicated were simultaneously added.

Cyan=Hoechst Arrows=Multinucleated Osteoclasts (b) Quantification of a.” • Thanks. 2c has now been corrected to “reduced” rather than the errant “oxidized”.

(4) How do authors normalize bone resorption, % of total area?  

- We normalized to a separate, paired well where monocytes are differentiated to precursors (MCSF), but no RANKL is added. We have added this omitted information to the methods sections for our mineral resorption assay.

(5) Figure 5. There are two legends (b). In Figure 5c RT-qPCR, the DC-STAMP or OC-STAMP and mature osteoclast marker calcitonin receptor should be included.

- Thank you. There were several problems with Figure legend 5 that both you and Reviewer #1 brought our attention to. We have now corrected these errors.

- We understand the Reviewer’s interest in these markers. However, our point is that the steadystate transcript levels of two well recognized osteoclast differentiation factors and the fusion regulator La, which our manuscript focuses on, are not significantly altered by NAC treatment at these later, fusion associated timepoints. While DC-STAMP, OC-STAMP, and Calcitonin would be interesting, we believe they are outside the scope of this manuscript.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

HMGCS1, 3-hydroxy-3-methylglutaryl-CoA synthase1 is predicted to be involved in Acetyl-CoA metabolic process and mevalonate-cholesterol pathway. To induce diet-induced diabetes, they fed wild-type littermates either a standard chow (Control) or a high fat-high sucrose (HFHG) diet, where the diet composition consisted of 60% fat, 20% protein, and 20% carbohydrate (H10060, Hfkbio, China). The dietary regimen was maintained for 14 weeks. Throughout this period, body weight and fasting blood glucose (FBG) levels were measured on a weekly basis. Although the authors induced diabetes with a diet also rich in fat, the cholesterol concentration or metabolism was not investigated. After the treatment, were the animals with endothelial dysfunction? How was the blood pressure of the animals?

Thank you for your comments and kind suggestions. We have conducted a study on the impact of HFHG diet on the serum levels of total cholesterol(T-CHO) in mice over a 14-week period. Our findings indicated that the HFHG diet significantly elevated T-CHO levels in the serum of mice (Supplementary Figure 5E). Additionally, HFHG diet was associated with an increased in blood pressure (Figure 5F) and it exacerbated the progression of endothelial dysfunction in mice (Figure 5H-L).

Strengths:

To explore the potential role of circHMGCS1 in regulating endothelial cell function, the authors cloned exons 2-7 of HMGCS1 into lentiviral vectors for ectopic overexpression of circHMGCS1 (Figure S2). The authors could use this experiment as a concept proof and investigate the glucose concentration in the cell culture medium. Is the pLV-circ HMGCS1 transduction in HUVEC increasing the glucose release? (Line 163)

In the manuscript, we utilized a DMEM culture medium containing 4500 mg/L glucose. Given that the HUVEC cell culture is glucose-dependent for its metabolic processes, it was challenging to precisely evaluate the relationship between pLV-circHMGCS1 transduction and the glucose concentration in the medium.

Weaknesses:

(1) Pg 20. The cells were transfected with miR-4521 mimics, miR-inhibitor, or miR-NC and incubated for 24 hours. Subsequently, the cells were treated with PAHG for another 24 hours. Were the cells transfected with lipofectanine? The protocol or the lipofectamine kit used should be described. The lipofectamine protocol suggests using an incubation time of 72 hours. Why did the authors incubate for only 24 hours? If the authors did the mimic and inhibitor curves, these should be added to the supplementary figures. Please, describe the miRNA mimic and antagomir concentration used in cell culture.

For detailed transfection methods of miRNA mimic and its inhibitor, please refer to “Transfection of miRNA mimic or inhibitor” (Line 587) in the revised Experimental Section. We employed the Hieff Trans®siRNA/miRNA in vitro transfection reagent (yeason, China, 40806ES03), with a transfection duration of 48h. The miR-4521 content in HUVEC post-transfection was quantified using qRT-PCR. The transfection of the miR-4521 mimic for 48h notably enhanced its expression in HUVEC (Supplementary Figure 3B), whereas the transfection of the miR-4521 inhibitor for the same duration significantly suppressed its expression (Supplementary Figure 3C). The concentration used for both miRNA mimic and inhibitor transfection was 50 nM. In the revised manuscript, we have corrected the transfection time and clarified that we did not utilize miRNA antagomirs in our experiments.

(2) Pg 20, line 507. What was the miR-4521 agomiR used to treatment of the animals?

miRNA agomir serves as a valuable experimental tool for elucidating miRNA function, used to simulate the overexpression of a specific miRNA. miRNA agomir is a chemically modified RNA molecule identical in sequence to the target miRNA, engineered for enhanced stability and transfection efficacy. Utilizing miRNA agomir enables the overexpression of the target miRNA, facilitating the investigation of miRNA functions and mechanism in vivo. In our study, we have employed miRNA mimic for cellular studies and miRNA agomir in vivo applications to achieve high expression of miRNA (Fu et al, 2019).

(3) Figure 1B. The results are showing the RT-qPCR for only 5 circRNA, however, the results show 48 circRNAs were upregulated, and 18 were downregulated (Figure S1D). Why were the other cicRNAs not confirmed? The circRNAs upregulated with high expression are not necessarily with the best differential expression comparing control vs. PAHG groups. Furthermore, Figure 1A and S1D show circRNAs downregulated also with high expression. Why were these circRNAs not confirmed?

Our study aims to the identification of potential biomarkers for endothelial dysfunction in type 2 diabetes, To the end, we focused on circRNAs that exhibited significant upregulation following PAHG treatment. In our sequencing data, the p-values for these top upregulated circRNAs were notably below the threshold of 0.001, prompting their selection for further validation. We employed qRT-PCR to ascertain the consistency of their expression levels with the RNA-sequencing findings. Among these, circHMGCS1 was identified as a promising candidate with regulatory potential in endothelial dysfunction. Additionally, circRNAs that were significantly downregulated will be the subject of our ongoing research endeavors.

(4) Figure 1B shows the relative circRNAs expression. Were host genes expressed in the same direction?

circRNAs are generated from specific exons or introns of their host genes, either individually or in combination, and the main function of circRNA depends on its non-coding RNA characteristics. The expression levels of circRNAs is not necessarily correlated with those of their host genes, and similarly, the function of circRNAs do not inherently relate to the functions of the host genes (Kristensen et al, 2019; Liu & Chen, 2022). Consequently, the data presented in Figure 1B were primarily aimed at validating the accuracy of circRNA-seq. Although we did not conduct host gene expression analysis for the identified circRNAs, our subsequent results indicated that the overexpression of circHMGCS1 did not influence the expression levels of HMGCS1 (Figure 2A).

(5) Line 128. The circRNA RT-qPCR methodology was not described. The methodology should be described in detail in the Methods Session.

The only difference between the circRNA RT-qPCR method and other gene detection is that random primers need to be used for reverse transcription during the reverse transcription process. Unlike linear RNAs that possess a 3' polyA tail, which allows for the use of oligo(dT) primers, circRNAs require random primers to initiate the reverse transcription process. Beyond this distinction, the other processes are no different from the common qRT-PCR process. We have revised the Isolation of RNA and miRNA for quantitative Real Time-PCR (qRT-PCR) analysis method in the revised version (Line 695).

(6) Line 699. The relative gene expression was calculated using the 2-ΔΔCt method. This is not correct, the expression for miRNA and gene expression are represented in percentage of control.

We initially employed the 2^-ΔΔCt method to ascertain the relative gene expression levels. Subsequently, we scaled all values by a factor of 100 to amplify the visual representation of the observed variations, thereby enhancing the visualization of the data.

(7) Line 630. Detection of ROS for tissue and cells. The methodology for tissue was described, but not for cells.

We have added the detailed description of the cellular ROS detection methods in the revised manuscript as follows:

For ROS detection in cells, the treated cells were washed once by PBS, then 20 μM DHE was added, and incubated at 37°C for 30 min away from light, then washed three times by PBS and then colorless DMEM medium was added, followed by fluorescence microscopy for observation (Line 640-643).

(8) Line 796. RNA Fluorescent In Situ Hybridization (RNA-FISH). Figure 1F shows that the RNA-Fluorescence in situ hybridization (RNA-FISH) confirmed the robust expression of cytoplasmic circHMGCS1 in HUVECs (Figure 1F). However, in the methods, lines 804 and 805 described the probes targeting circMAP3K5 and miR-4521 were applied to the sections. Hybridization was performed in a humid chamber at 37C overnight. Is it correct?

We have made a correction in the revised manuscript. The accreted description is "the probes targeting circHMGCS1 and miR-4521 were applied to the sections"(Line816).

(9) Line 14. Fig 1-H. The authors discuss qRT-PCR demonstrated that circHMGCS1 displayed a stable half-life exceeding 24 h, whereas the linear transcript HMGCS1 mRNA had a half-life less than 8 h (Figure 1H). Several of the antibodies may contain trace amounts of RNases that could degrade target RNA and could result in loss of RNA hybridization signal or gene expression. Thus, all of the solutions should contain RNase inhibitors. The HMGCS1 mRNA expression could be degraded over the incubation time (0-24hs) leading to incorrect results. Moreover, in the methods is not mentioned if the RNAse inhibitor was used. Please, could the authors discuss and provide information?

This experiment was performed in cell culture as described in our Experimental Methods (Line 753), where we added actinomycin D directly into the cell culture well plates, and the cells remained in a healthy state during this treatment. We did not directly extract mRNA from cells for this experiment. Additionally, all solutions utilized throughout the whole experiment were prepared using Rnase-free water, ensuring that the integrity of the mRNA.

(10) Further experiments demonstrated that the overexpression of circHMGCS1 stimulated the expression of adhesion molecules (VCAM1, ICAM1, and ET-1) (Figures 2B and 2C), suggesting that circHMGCS1 is involved in VED. How were these genes expressed in the RNA-seq?

In the manuscript, we only focused exclusively on circRNA and miRNA sequencing, and not perform mRNA sequencing, Consequently, we employed qRT-PCR and Western blot to assess the expression alterations of ET-1, ICAM1, and VCAM1 at gene and protein level. The findings revealed that the overexpression of circHMGCS1 significantly upregulated the expression of adhesion molecules (VCAM1, ICAM1, and ET-1).

(11) Line 256. By contrast, the combined treatment of circHMGCS1 and miR-4521 agomir did not significantly affect the body weight and blood glucose levels. OGTT and ITT experiments demonstrated that miR-4521 agomir considerably enhanced glucose tolerance and insulin resistance in diabetic mice (Figures 5C, 5D, and Figures S5B and S5C). Why did the miR-4521 agomir treatment considerably enhance glucose tolerance and insulin resistance in diabetic mice, but not the blood glucose levels?

Our results showed that miR-4521 agomir could effectively suppress the increase of body weight and blood glucose in mice (Figure 5A-B).

(12) In the experiments related to pull-down, the authors performed Biotin-coupled miR-4521 or its mutant probe, which was employed for circHMGCS1 pull-down. This result only confirms the Luciferase experiments shown in Figure 4A. The experiment that the authors need to perform is pull-down using a biotin-labeled antisense oligo (ASO) targeting the circHMGCS1 backsplice junction sequence followed by pulldown with streptavidin-conjugated magnetic beads to capture the associated miRNAs and RNA binding proteins (RBPs). Also, the ASO pulldown assay can be coupled to miRNA RT-qPCR and western blotting analysis to confirm the association of miRNAs and RBPs predicted to interact with the target circRNA.

This point is correct. As suggested, we utilized a biotin-labeled circHMGCS1 probe for pull down experiments. Because circRNA-miRNA interactions are mainly mediated by the RNA-induced silencing complex, which includes Argonaute 2 (AGO2), we examined the levels of miR-4521 and AGO2 in the capture meterial. Our results demonstrated that circHMGCS1 significantly captured miR-4521 in the cells, with a concomitant acquisition of AGO2. These findings have been integrated into the revised manuscript (Supplementary Figures 4D and 4E).

(13) In Figure 5, the authors showed that the results suggest that miR-4521 can inhibit the occurrence of diabetes, whereas circHMGCS1 specifically dampens the function of miR-4521, weakening its protective effect against diabetes. In this context, what are the endogenous target genes for the miR-4521 that could be regulating diabetes?

In this study, we focused on the role of miR-4521 in endothelial function. Our animal experiments involving ARG1 knockdown revealed that the reduction of ARG1 expression resulted in the inability of miR-4521 to modulate the progression of type 2 diabetes. Consequently, ARG1 is likely an endogenous target gene of miR-4521, potentially implicated in the regulation of diabetes.

(14) In the western blot of Figure 5, the β-actin band appears to be different from the genes analyzed. Was the same membrane used for the four proteins? The Ponceau S membrane should be provided.

As described in our experimental methodology (Western blot analysis), we have utilized PVDF membranes for our Western blot experiments. β-actin, recognized for its high expression and specificity as a housekeeping gene, yields distinct bands with minimal background noise. This property can lead to the migration β-actin from the spot wells to both sides during electrophoresis. So much so that it is not aligned with the lane shown by the target gene. And the other 3 genes can see the phenomenon of obvious lane because their expression is not as high as β-actin. We replaced β-actin with a similar background in the revised manuscript (Figure 5L).

(15) Why did the authors use AAV9, since the AAV9 has a tropism for the liver, heart, skeletal muscle, and not to endothelial vessels?

AAV9 has garnered significant interest as a gene delivery vector due to its extensive tissue penetration, minimal immunogenicity, and stable gene expression profile. Its application in cardiovascular disease research and therapy has been widely reported (Barbon et al, 2023; Yao et al, 2018; Zincarelli et al, 2008). Meanwhile, we employed AAV9 for gene delivery via the tail vein injection in mice, and as shown in Figure 5J and Figure 7Q, we observed GFP signals carried by AAV9 in the thoracic aorta of mice. These findings suggest that AAV9 possesses the capability to infect endothelial cells effectively.

Reviewer #2 (Public Review):

Summary:

The authors observed an aggravated vascular endothelial dysfunction upon overexpressing circHMGCS1 and inhibiting miR-4521. This study discovered that circHMGCS1 promotes arginase 1 expression by sponging miR-4521, which accelerated the impairment of vascular endothelial function.

Strengths:

The study is systematic and establishes the regulatory role of the circHMGCS1-miR-4521 axis in diabetes-induced cardiovascular diseases.

Weaknesses:

(1) The authors selected the miR-4521 as the target based on their reduced expression upon circHMGCS1 overexpression. Since the miRNA level is downregulated, the downstream target gene is expected to be upregulated even in the absence of circRNA. The changes in miRNA expression opposite to the levels of target circRNA could be through Target RNA-Directed MicroRNA Degradation. In addition, miRNA can also be stabilized by circRNAs. Hence, selecting miRNA targets based on opposite expression patterns and concluding miRNA sponging by circRNA needs further evidence of direct interactions.

Thank you for your positive comments and kind suggestions.

As suggested by Public Reviewer #1 (12), we employed a biotin-tagged circHMGCS1 to capture miR-4521 and AGO2 in HUVECs (Supplementary Figures 4D and 4E), and Dual luciferase assays have confirmed that miR-4521 can bind to circHMGCS1 directly. Furthermore, RNA pull down and RIP assays have demonstrated the direct binding capability of circHMGCS1 for miR-4521. Collectively, these findings underscore the direct interaction between circHMGCS1 and miR-4521.

(2) The majority of the experiments were performed with an overexpression vector which can generate a lot of linear RNAs along with circRNAs. The linear RNAs produced by the overexpression vectors can have a similar effect to the circRNA due to sequence identity.

In our manuscript, the employed vectors incorporate reverse repeat sequences that facilitate efficient circularization of circRNAs. This design ensures robust circular shearing upon the insertion of circRNA sequences into the polyclonal sites, thereby enhancing the overexpression of circRNAs (Supplementary Figure 2). Moreover, we used lentiviral virus as a vector for circRNA overexpression, not direct plasmid transfection. As demonstrated in Figure 2A, upon overexpression of circHMGCS1, we observed a significant upregulation in circHMGCS1 levels compared to the pLV-circNC and Control groups. Notably, the expression levels of the linear HMGCS1 mRNA did not exhibit significant alterations.

(3) There is a lack of data of circHMGCS1 silencing and its effect on target miRNA & mRNAs.

According to your suggestion, we employed shRNA to knockdown circHMGCS1 in HUVEC, and qRT-PCR was used to assess the expression levels of miR-4521 and ARG1. The knockdown of circHMGCS1 significantly inhibit the expression of circHMGCS1 in HUVEC without obviously affecting the levels of HMGCS1 mRNA. We then selected circHMGCS1 shRNA1 for further investigation. We observed that the knockdown of circHMGCS1 resulted in an upregulation of miR-4521 and a downregulation of ARG1 expression.

Author response image 1.

The impact of circHMGCS1 knockdown on ARG1 and miR-4521 expression levels in HUVEC. The cells were transfected with either circHMGCS1 shRNA1 or circHMGCS1 shRNA2, and the expressions levels of circHMGCS1 and HMGCS1 (A), miR-4521 (B) and ARG1 (C and D) in HUVECs were detected by qRT-PCR and Western blot. n=3 in each group. *p < 0.05, **p < 0.01. All significant difference was determined by one-way ANOVA followed by Bonferroni multiple comparison post hoc test, error bar indicates SD.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I suggest improving the discussion based on the literature.

(1) Line 131. .... (hsa_circ_0008621, 899 nt in length, identified as circHMGCS1 in subsequent studies because of its host gene being HMGCS1). Please, provide the reference.

We appreciate the valuable comments. We have made changes for improvement, which is add in Line 133(Liang et al, 2021).

(2) The authors conclude that both in vitro and in vivo data suggest that the miR-4521 or circHMGCS1 fails to regulate the effect of diabetes-induced VED in the absence of ARG1. Therefore, ARG1 may serve as a promising VED biomarker, and circHMGCS1 and miR-4521 play a key role in regulating diabetes-induced VED by ARG1. In this context, they should re-evaluate whether this is the best title. "Circular RNA HMGCS1 sponges miR-4521 to aggravate type 2 diabetes-induced vascular endothelial dysfunction"

This manuscript initiates its exploration with circRNA as the focal point of study (Figure 1 and Figure 2), It then delves into the miRNAs associated with circRNA and elucidates their interactions (Figure 3, Figure 4 and Figure 5). Subsequently, the manuscript identifies the target genes of miRNA and validates the regulatory effects of circRNA and miR-4521 on ARG1 (Figure 6). The study culminates with the application of the ceRNA theory to confirm the significance of ARG1 in the functional interplay between circHMGCS1 and miR-4521 (Figure 7). These findings throughout the manuscript are dedicated to uncovering the pivotal roles of circHMGCS1 and miR-4521 in modulating vascular endothelial function. Notably, the interaction between circHMGCS1 and miR-4521 represents a novel discovery of our research. Therefore, we aim to emphasize the critical function of circHMGCS1 and miR-4521 in the regulation of vascular endothelial dysfunction in type 2 diabetes within the manuscript.

Reviewer #2 (Recommendations For The Authors):

I have a few suggestions for improving the study further.

(1) Although the experiments suggest the role of circHMGCS1, miR-4521 in vascular endothelial function, the direct regulation or interaction of circHMGCS1-miR-4521-ARG1 is unclear. A rescue experiment that checks the effect of circHMGCS1 silencing with/without inhibition of miR-4521 on ARG1 expression must be performed to prove the circHMGCS1- miR-4521 regulatory axis.

Thank you very much for your constructive comments.

According to your suggestion, we utilized shRNA to effectively knockdown circHMGCS1 in HUVEC, Subsequent expression analysis via qRT-PCR was conducted to assess the levels of miR-4521 and ARG1. The knockdown of circHMGCS1 significantly reduced the expression of circHMGCS1 in HUVEC without influencing the expression of the host gene HMGCS1. Concurrently, the knockdown of circHMGCS1 resulted in an upregulation of miR-4521 (Supplementary Figure 4B) and a downregulation of ARG1 (Figure 6P and 6Q). In our manuscript, the upregulation in ARG1 expression caused by circHMGCS1 overexpression was reduced by miR-4521, and the downregulation in ARG1 expression caused by miR-4521 overexpression was also reversed by circHMGCS1. When miR-4521 was knocked down, the expression of ARG1 increased, and circHMGCS1 abrogated its regulatory effect on the expression of ARG1. Collectively, these findings indicate that the interplay between circHMGCS1 and miR-4521 significantly influences ARG1 expression.

Author response image 2.

The impact of circHMGCS1 knockdown on ARG1 and miR-4521 expression levels in HUVEC. The cells were transfected with either circHMGCS1 shRNA1 or circHMGCS1 shRNA2, and the expressions levels of circHMGCS1 and HMGCS1 (A), miR-4521 (B) and ARG1 (C and D) in HUVECs were detected by qRT-PCR and Western blot. n=3 in each group. *p < 0.05, **p < 0.01. All significant difference was determined by one-way ANOVA followed by Bonferroni multiple comparison post hoc test, error bar indicates SD.

(2) It is unclear how the authors arrived at the circHMGCS1-miR-4521 pair. The pull down of circHMGCS1 followed by qPCR enrichment analysis of all target miRNAs must be performed to select the target miRNA.

In this manuscript, we identified the expression of miRNA under PAHG treatment through miRNA sequencing, and then further screened out 4 miRNAs with potential binding sites to circHMGCS1 utilizing the miRanda database. Subsequently, we employed qRT-PCR and Western blot analysis to confirm the regulatory influence of miR-4521 on endothelial function (Figure 3). Following this, RIP, RNA pull down, dual luciferase and RNA-FISH experiments were conducted to map the interaction between circHMGCS1 and miR-4521 (Figure 4), the direct interaction between circHMGCS1 and miR-4521 was further substantiated through overexpression and knockdown studies (Figures 5-7). while the reviewer's method may offer a more direct validation, our methodology initially involved a database-driven screening of candidate miRNAs with the potential to target and bind circHMGCS1, followed by experimental validation of these interactions. Both methodologies are capable of establishing the interaction sites between circHMGCS1 and miR-4521.

(3) Since the back splicing is not that efficient, the linear RNA from the overexpression construct may produce many linear RNAs with miRNA binding sites. The effect seen in the case of overexpression experiments needs to consider the level of linear and circular HMGCS1 produced by the vector.

In this manuscript, the vector's multiple cloning site is flanked by inverted repeat sequences that facilitate efficient circRNA looping. This design enables the inserted sequence to form a stable loop and undergo circularization upon transcription, leading to the overexpression of circRNA (Supplementary Figure 2). For the validation of circular RNA, we employed divergent primers that straddle the circRNA splicing junction. These primers are specific for circRNA amplification and do not amplify the corresponding linear RNA, as demonstrated in Figure 2A. Upon overexpression of circHMGCS1, we observed a significant increase in circHMGCS1 levels compared to the empty vector and Control groups, while there was no significant change in the expression level of HMGCS1 mRNA.

(4) As miR-4521 has multiple miRNA binding sites on circHMGCS1, it is not very clear which sites were mutated in circHMGCS1-MUT.

We have made corrections to Supplementary Figure 4C. Utilizing the miRanda algorithm, we identified 10 potential binding sites for miR-4521 on circHMGCS1. Subsequently, we selected the site with the highest binding affinity for mutational analysis (miR-4521 binding positions 3-15, circHMGCS1 binding positions 260-281, binding rate 91.67%, binding ability -17.299999 kCal/Mol). We employed a dual-luciferase assay to confirm the direct interaction between circHMGCS1 and miR-4521.

(5) Since the ceRNA network works efficiently in an equimolar concentration of the regulatory molecules, providing the copy number of circHMGCS1, miR-4521, and target mRNAs would be helpful.

We employed qRT-PCR to ascertain the absolute quantification of mRNA copy numbers, following established methodologies (Nolan et al, 2006; Wagatsuma et al, 2005; Zhang et al, 2009). Our qRT-PCR data reveal that the circHMGCS1 mRNA copy number is 2343±529. In comparison, the ARG1 mRNA copy number stands at 88±27, while the miR-4521 copy number is significantly higher, recorded at 36277±9407.

Author response image 3.

The distribution of copy numbers for circHMGCS1, miR-4521 and ARG1 in HUVECs.

(6) The yellow highlighted "cyclization-mediated sequence-F & R" does not seem to be complementary sequences. The method section may include the details of the vectors and cloning strategies for the overexpression constructs.

The figure below illustrates the schematic representation of the complementary structure between the upstream and downstream sequences that facilitate circRNA circularization. This strategic pairing is designed to enhance the circularization efficiency of circRNA while concurrently suppressing mRNA synthesis (Liang & Wilusz, 2014). Details of this design have been integrated into the experimental method (Line539). The specific additions are as follows:

The circHMGCS1 sequence [NM_001098272: 43292575-43297268], the splice site AG/GT and ALU elements were inserted into the pCDH-circRNA-GFP vector (upstream ALU: AAAGTGCTGAGATTACAGGCGTGAGCCACCACCCCCGGCCCACTTTTTGTAAAGGTACGTACTAATGACTTTTTTTTTATACTTCAG, downstream ALU: GTAAGAAGCAAGGAAAAGAATTAGGCTCGGCACGGTAGCTCACACCTGTAATCCCAGCA). The restriction enzyme sites selected were EcoRI and NotI.

Author response image 4.

(7) Since circHMGCS1 is a multi-exonic circRNA that can undergo alternative splicing and divergent primers only validate the backsplice junction, the full-length sequence of mature circHMGCS1 needs to be checked by circRNA-RCA PCR followed by Sanger sequencing.

In compliance with your guidance, we have enriched the revised manuscript with additional data. Specifically, we have included the full-length nucleic acid electrophoresis diagram of circHMGCS1 in Supplementary Figure 1F, the Sanger sequencing results in Supplementary Figure 1G, and a comparative analysis of the circHMGCS1 sequences obtained from Sanger sequencing with those referenced in the circBase database, presented in Supplementary Figure 1H.

Reference:

Barbon, E., C. Kawecki, S. Marmier, A. Sakkal, F. Collaud, S. Charles, G. Ronzitti, C. Casari, O.D. Christophe, C.V. Denis, P.J. Lenting, and F. Mingozzi. 2023. Development of a dual hybrid AAV vector for endothelial-targeted expression of von Willebrand factor. Gene Ther. 30: 245-254.

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Kristensen, L.S., M.S. Andersen, L.V.W. Stagsted, K.K. Ebbesen, T.B. Hansen, and J. Kjems. 2019. The biogenesis, biology and characterization of circular RNAs. Nat Rev Genet. 20: 675-691.

Liang, D., and J.E. Wilusz. 2014. Short intronic repeat sequences facilitate circular RNA production. Genes Dev. 28: 2233-2247.

Liang, J., X. Li, J. Xu, G.M. Cai, J.X. Cao, and B. Zhang. 2021. hsa_circ_0072389, hsa_circ_0072386, hsa_circ_0008621, hsa_circ_0072387, and hsa_circ_0072391 aggravate glioma via miR-338-5p/IKBIP. Aging (Albany NY). 13: 25213-25240.

Liu, C.X., and L.L. Chen. 2022. Circular RNAs: Characterization, cellular roles, and applications. Cell. 185: 2016-2034.

Nolan, T., R.E. Hands, and S.A. Bustin. 2006. Quantification of mRNA using real-time RT-PCR. Nat Protoc. 1: 1559-1582.

Wagatsuma, A., H. Sadamoto, T. Kitahashi, K. Lukowiak, A. Urano, and E. Ito. 2005. Determination of the exact copy numbers of particular mRNAs in a single cell by quantitative real-time RT-PCR. J Exp Biol. 208: 2389-2398.

Yao, C., T. Veleva, L. Scott, Jr., S. Cao, L. Li, G. Chen, P. Jeyabal, X. Pan, K.M. Alsina, I.D. Abu-Taha, S. Ghezelbash, C.L. Reynolds, Y.H. Shen, S.A. Lemaire, W. Schmitz, F.U. Müller, A. El-Armouche, N. Tony Eissa, C. Beeton, S. Nattel, X.H.T. Wehrens, D. Dobrev, and N. Li. 2018. Enhanced Cardiomyocyte NLRP3 Inflammasome Signaling Promotes Atrial Fibrillation. Circulation. 138: 2227-2242.

Zhang, X.X., T. Zhang, M. Zhang, H.H. Fang, and S.P. Cheng. 2009. Characterization and quantification of class 1 integrons and associated gene cassettes in sewage treatment plants. Appl Microbiol Biotechnol. 82: 1169-1177.

Zincarelli, C., S. Soltys, G. Rengo, and J.E. Rabinowitz. 2008. Analysis of AAV serotypes 1-9 mediated gene expression and tropism in mice after systemic injection. Mol Ther. 16: 1073-1080.

Author response:

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this work, the authors continue their investigations on the key role of glycosylation to modulate the function of a therapeutic antibody. As a follow-up to their previous demonstration on how ADCC was heavily affected by the glycans at the Fc gamma receptor (FcγR)IIIa, they now dissect the contributions of the different glycans that decorate the diverse glycosylation sites. Using a well-designed mutation strategy, accompanied by exhaustive biophysical measurements, with extensive use of NMR, using both standard and newly developed methodologies, they demonstrate that there is one specific locus, N162, which is heavily involved in the stabilization of (FcγR)IIIa and that the concomitant NK function is regulated by the glycan at this site.

Strengths:

The methodological aspects are carried out at the maximum level.

Weaknesses:

The exact (or the best possible assessment) of the glycan composition at the N162 site is not defined.

We will revise the Introduction to include previous findings from our laboratory regarding processing on YTS cells:

“YTS cells, a key cytotoxic human NK cell line used for these studies, express FcγRIIIa with extensive glycan processing, including the N162 site with predominantly hybrid and complex-type glycoforms {Patel 2021}.”  

Reviewer #2 (Public Review):

Summary:

The authors set out to demonstrate a mechanistic link between Fcgamma receptor (IIIA) glycosylation and IgG binding affinity and signaling - resulting in antibody-dependent cellular cytotoxicity - ADCC. The work builds off prior findings from this group about the general impact of glycosylation on FcR (Fc receptor)-IgG binding.

Strengths:

The structural data (NMR) is highly compelling and very significant to the field. A demonstration of how IgG interacts with FcgRIIIA in a manner sensitive to glycosylation of both the IgG and the FcR fills a critical knowledge gap. The approach to demonstrate the selective impact of glycosylation at N162 is also excellent and convincing. The manuscript/study is, overall, very strong.

Weaknesses:

There are a number of minor weaknesses that should be addressed.

(1) Since S164A is the only mutant in Figure 1 that seems to improve affinity, even if minimally, it would be a nice reference to highlight that residue in the structural model in panel B.

We will revise Figure 1B to include the S164 site.

(2) It is confusing why some of the mutants in the study are not represented in Figure 1 panel A. Those affinities and mutants should be incorporated into panel A so the reader can easily see where they all fall on the scale.

We thank the reviewer for this comment. We will restructure the Results section to highlight that a primary outcome of the experiment referenced was to map the contribution of interface residues to antibody binding affinity. These data were not previously available, highlighting hotspots at the interface. Figure 1A and B report these results.

We then used a subset of mutations from this experiment, as well as a subset of mutations from an additional library containing mutations proximal to the interface, to build a small library for evaluation using ADCC. The complete binding data for all variants, binding to two different IgG1 Fc glycoforms, is presented in Supplemental Table 1. 

T167Y in particular needs to be shown, as it is one of few mutants that fall between what seems to be ADCC+ and ADCC- lines. Also, that mutant seems to have a stronger affinity compared to wt (judged by panel D), yet less ADCC than wt. This would imply that the relationship between affinity and activity is not as clean as stated, though it is clearly important. Comments about this would strengthen the overall manuscript.

We thank the reviewer for this particular insight. We agree that the lack of a clean correlation between ADCC potency and affinity implies additional factors that could have affected these experimental results. We will add the following sentence to the discussion. 

“Notably, the ADCC potency for those high-affinity variants does not fall cleanly on a line, indicating that other factors affect our observations, which may include organization at the cell surface, changes to glycan composition, or receptor trafficking.”

(3) This statement feels out of place: "In summary, this result demonstrates that the sensitivity to antibody fucosylation may be eliminated through FcγRIIIa engineering while preserving antibody-binding affinity." In Figure 2, the authors do indeed show that mutations in FcgRIIIa can alter the impact of IgG core fucosylation, but implying that receptor engineering is somehow translatable or as impactful therapeutically as engineering the antibody itself deflates the real basic science/biochemical impact of understanding these interactions in molecular detail. Not everything has to be immediately translatable to be important. 

We agree and will remove the highlighted sentence.   

(4) The findings reported in Figure 2, panel C are exciting. Controls for the quality of digestion at each step should be shown (perhaps in supplementary data). We agree.

We will add an example of the digestions as Figure S2.  

(5) Figure 3 is confusing (mislabeled?) and does not show what is described in the Results. First, there is a F158V variant in the graph but a V158F variant in the text.

Please correct this. 

Thank you for identifying this typo. We will correct Figure 3.

Second, this variant (V158F/F158V) does not show the 2-fold increase in ADCC with kifunesine as stated. 

Thank you for drawing our attention to this rounding error. We will revise the text to report a statistically significant 1.4-fold increase.

Finally, there are no statistical evaluations between the groups (+/- kif; +/- fucose). 

We provide the p values for +/-fuc and +/- Kifunensine for each YTS cell line in the figure. We did not provide a global comparison of p values that included all cell lines due to some cell lines experiencing a significant change and others not. However, we will add the raw data as Supplemental Table 2 should readers wish to perform these analyses.

The differences stated are not clearly statistically significant given the wide spread of the data. This is true even for the wt variant.

We agree that there are points that overlap in this figure between the different treatments. However, our use of the students T-test (two tailed) using three experiments collected on three different days (each with three technical replicates) provides enough resolution to determine the significance of difference of the means for the different treatments. This is, by our estimation, a highly rigorous manner to collect and analyze the data.  

(6) The kifunensine impact is somewhat confusing. They report a major change in ADCC, yet similar large changes with trimming only occur once most of the glycan is nearly gone (Figure 2). Kifunensine will tend to generate high mannose and possibly a few hybrid glycans. It is difficult to understand what glycoforms are truly important outside of stating that multi-branched complex-type N-glycans decrease affinity.

Note that Figure 2 does not evaluate the kifunensine-treated glycan, which is mostly Man8 and Man9 structures. In our previous work, these structures likewise provide increased binding affinity (see pubmed ID 30016589). We believe the most important message is that composition of the N162 glycan (removed with the S164A mutation) regulates NK cell ADCC. On cells, we are not able to modulate N162 glycan composition without affecting potentially every other N-glycan on the surface, so we do not have an ADCC experiments that is directly comparable to Figure 2. Thus, this increased ADCC resulting from kifunensine treatment is consistent with previously observed increases in binding affinity measurement.  

(7) This is outside of the immediate scope, but I feel that the impact would be increased if differences in NK cell (and thus FcgRIIIA) glycosylation are known to occur during disease, inflammation, age, or some other factor - and then to demonstrate those specific changes impact ADCC activity via this mechanism.

We agree completely. As mentioned in the Introduction, we know that N162 glycan composition varies substantially from donor to donor based on previous work from our lab. Curiously, little variability appeared between donors at the other four Nglycosylation sites. Thus, there is the potential that different NK cell N162 glycan compositions are coincident with different indications. This is an area we are quite interested in pursuing.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this manuscript, the authors investigate the contributions of the long noncoding RNA snhg3 in liver metabolism and MAFLD. The authors conclude that liver-specific loss or overexpression of Snhg3 impacts hepatic lipid content and obesity through epigenetic mechanisms. More specifically, the authors invoke that the nuclear activity of Snhg3 aggravates hepatic steatosis by altering the balance of activating and repressive chromatin marks at the Pparg gene locus. This regulatory circuit is dependent on a transcriptional regulator SND1.

Strengths:

The authors developed a tissue-specific lncRNA knockout and KI models. This effort is certainly appreciated as few lncRNA knockouts have been generated in the context of metabolism. Furthermore, lncRNA effects can be compensated in a whole organism or show subtle effects in acute versus chronic perturbation, rendering the focus on in vivo function important and highly relevant. In addition, Snhg3 was identified through a screening strategy and as a general rule the authors the authors attempt to follow unbiased approaches to decipher the mechanisms of Snhg3.

Weaknesses:

Despite efforts at generating a liver-specific knockout, the phenotypic characterization is not focused on the key readouts. Notably missing are rigorous lipid flux studies and targeted gene expression/protein measurement that would underpin why the loss of Snhg3 protects from lipid accumulation. Along those lines, claims linking the Snhg3 to MAFLD would be better supported with careful interrogation of markers of fibrosis and advanced liver disease. In other areas, significance is limited since the presented data is either not clear or rigorous enough. Finally, there is an important conceptual limitation to the work since PPARG is not established to play a major role in the liver.

We thank the reviewer for the detailed comment. In this study, hepatocyte-specific Snhg3 deficiency decreased body and liver weight and alleviated hepatic steatosis in DIO mice, whereas overexpression induced the opposite effect (Figure 2 and 3). Furthermore, we investigated the hepatic differentially expressed genes (DEGs) between the DIO Snhg3-HKI and control WT mice using RNA-Seq and revealed that Snhg3 exerts a global effect on the expression of genes involved in fatty acid metabolism using GSEA (Figure 4B). We validated the expression of some DEGs involved in fatty acid metabolism by RT-qPCR. The results showed that the hepatic expression levels of some genes involved in fatty acid metabolism, including Cd36, Cidea/c and Scd1/2 were upregulated in Snhg3-HKO mice and were downregulated in Snhg3-HKI mice compared to the controls (Figure 4C), respectively. Please check them in the first paragraph in p8.

As a transcription regulator of Cd36 and Cidea/c, it is well known that PPARγ plays major adipogenic and lipogenic roles in adipose tissue. Although the expression of PPARγ in the liver is very low under healthy conditions, induced expression of PPARγ in both hepatocytes and non-parenchymal cells (Kupffer cells, immune cells, and HSCs) in the liver has a crucial role in the pathophysiology of MASLD (Lee et al., 2023b, Chen et al., 2023, Gross et al., 2017). The activation of PPARγ in the liver induces the adipogenic program to store fatty acids in lipid droplets as observed in adipocytes (Lee et al., 2018). Moreover, the inactivation of liver PPARγ abolished rosiglitazone-induced an increase in hepatic TG and improved hepatic steatosis in lipoatrophic AZIP mice (Gavrilova et al., 2003). Furthermore, there is a strong correlation between the onset of hepatic steatosis and hepatocyte-specific PPARγ expression. Clinical trials have also indicated that increased insulin resistance and hepatic PPARγ expressions were associated with NASH scores in some obese patients (Lee et al., 2023a, Mukherjee et al., 2022). Even though PPARγ’s primary function is in adipose tissue, patients with MASLD have much higher hepatic expression levels of PPARγ, reflecting the fact that PPARγ plays different roles in different tissues and cell types (Mukherjee et al., 2022). As these studies mentioned above, our result also hinted at the importance of PPARγ in the pathophysiology of MASLD. Snhg3 deficiency or overexpression respectively induced the decrease or increase in hepatic PPARγ. Moreover, administration of PPARγ antagonist T0070907 mitigated the hepatic Cd36 and Cidea/c increase and improved Snhg3-induced hepatic steatosis. However,  conflicting findings suggest that the expression of hepatic PPARγ is not increased as steatosis develops in humans and in clinical studies and that PPARγ agonists administration didn’t aggravate liver steatosis (Gross et al., 2017). Thus, understanding how the hepatic PPARγ expression is regulated may provide a new avenue to prevent and treat the MASLD (Lee et al., 2018). We also discussed it in revised manuscript, please refer the first paragraph in the section of Discussion in p13.

Hepatotoxicity accelerates the development of progressive inflammation, oxidative stress and fibrosis (Roehlen et al., 2020). Chronic liver injury including MASLD can progress to liver fibrosis with the formation of a fibrous scar. Injured hepatocytes can secrete fibrogenic factors or exosomes containing miRNAs that activate HSCs, the major source of the fibrous scar in liver fibrosis (Kisseleva and Brenner, 2021). Apart from promoting lipogenesis, PPARγ has also a crucial function in improving inflammation and fibrosis (Chen et al., 2023). In this study, no hepatic fibrosis phenotype was seen in Snhg3-HKO and Snhg3-HKI mice (figures supplement 1D and 2D). Moreover, deficiency and overexpression of Snhg3 respectively decreased and increased the expression of profibrotic genes, such as collagen type I alpha 1/2 (Col1a1 and Col1a2), but had no effects on the pro-inflammatory factors, including transforming growth factor β1 (Tgfβ1), tumor necrosis factor α (Tnfα), interleukin 6 and 1β (Il6 and Il1β) (figures supplement 3A and B). Inflammation is an absolute requirement for fibrosis because factors from injured hepatocytes alone are not sufficient to directly activate HSCs and lead to fibrosis (Kisseleva and Brenner, 2021). Additionally, previous studies indicated that exposure to HFD for more 24 weeks causes less severe fibrosis (Alshawsh et al., 2022). In future, the effect of Snhg3 on hepatic fibrosis in mice need to be elucidated by prolonged high-fat feeding or by adopting methionine- and choline deficient diet (MCD) feeding. Please check them in the second paragraph in the section of Discussion in p13.

References

ALSHAWSH, M. A., ALSALAHI, A., ALSHEHADE, S. A., SAGHIR, S. A. M., AHMEDA, A. F., AL ZARZOUR, R. H. & MAHMOUD, A. M. 2022. A Comparison of the Gene Expression Profiles of Non-Alcoholic Fatty Liver Disease between Animal Models of a High-Fat Diet and Methionine-Choline-Deficient Diet. Molecules, 27. DIO:10.3390/molecules27030858, PMID:35164140

CHEN, H., TAN, H., WAN, J., ZENG, Y., WANG, J., WANG, H. & LU, X. 2023. PPAR-gamma signaling in nonalcoholic fatty liver disease: Pathogenesis and therapeutic targets. Pharmacol Ther, 245, 108391. DIO:10.1016/j.pharmthera.2023.108391, PMID:36963510

GAVRILOVA, O., HALUZIK, M., MATSUSUE, K., CUTSON, J. J., JOHNSON, L., DIETZ, K. R., NICOL, C. J., VINSON, C., GONZALEZ, F. J. & REITMAN, M. L. 2003. Liver peroxisome proliferator-activated receptor gamma contributes to hepatic steatosis, triglyceride clearance, and regulation of body fat mass. J Biol Chem, 278, 34268-76. DIO:10.1074/jbc.M300043200, PMID:12805374

GROSS, B., PAWLAK, M., LEFEBVRE, P. & STAELS, B. 2017. PPARs in obesity-induced T2DM, dyslipidaemia and NAFLD. Nat Rev Endocrinol, 13, 36-49. DIO:10.1038/nrendo.2016.135, PMID:27636730

KISSELEVA, T. & BRENNER, D. 2021. Molecular and cellular mechanisms of liver fibrosis and its regression. Nat Rev Gastroenterol Hepatol, 18, 151-166. DIO:10.1038/s41575-020-00372-7, PMID:33128017

LEE, S. M., MURATALLA, J., KARIMI, S., DIAZ-RUIZ, A., FRUTOS, M. D., GUZMAN, G., RAMOS-MOLINA, B. & CORDOBA-CHACON, J. 2023a. Hepatocyte PPARgamma contributes to the progression of non-alcoholic steatohepatitis in male and female obese mice. Cell Mol Life Sci, 80, 39. DIO:10.1007/s00018-022-04629-z, PMID:36629912

LEE, S. M., MURATALLA, J., SIERRA-CRUZ, M. & CORDOBA-CHACON, J. 2023b. Role of hepatic peroxisome proliferator-activated receptor gamma in non-alcoholic fatty liver disease. J Endocrinol, 257. DIO:10.1530/JOE-22-0155, PMID:36688873

LEE, Y. K., PARK, J. E., LEE, M. & HARDWICK, J. P. 2018. Hepatic lipid homeostasis by peroxisome proliferator-activated receptor gamma 2. Liver Res, 2, 209-215. DIO:10.1016/j.livres.2018.12.001, PMID:31245168

MUKHERJEE, A. G., WANJARI, U. R., GOPALAKRISHNAN, A. V., KATTURAJAN, R., KANNAMPUZHA, S., MURALI, R., NAMACHIVAYAM, A., GANESAN, R., RENU, K., DEY, A., VELLINGIRI, B. & PRINCE, S. E. 2022. Exploring the Regulatory Role of ncRNA in NAFLD: A Particular Focus on PPARs. Cells, 11. DIO:10.3390/cells11243959, PMID:36552725

ROEHLEN, N., CROUCHET, E. & BAUMERT, T. F. 2020. Liver Fibrosis: Mechanistic Concepts and Therapeutic Perspectives. Cells, 9. DIO:10.3390/cells9040875, PMID:32260126

Reviewer #2 (Public Review):

Through RNA analysis, Xie et al found LncRNA Snhg3 was one of the most down-regulated Snhgs by a high-fat diet (HFD) in mouse liver. Consequently, the authors sought to examine the mechanism through which Snhg3 is involved in the progression of metabolic dysfunction-associated fatty liver diseases (MASLD) in HFD-induced obese (DIO) mice. Interestingly, liver-specific Snhg3 knockout was reduced, while Snhg3 over-expression potentiated fatty liver in mice on an HFD. Using the RNA pull-down approach, the authors identified SND1 as a potential Sngh3 interacting protein. SND1 is a component of the RNA-induced silencing complex (RISC). The authors found that Sngh3 increased SND1 ubiquitination to enhance SND1 protein stability, which then reduced the level of repressive chromatin H3K27me3 on PPARg promoter. The upregulation of PPARg, a lipogenic transcription factor, thus contributed to hepatic fat accumulation.

The authors propose a signaling cascade that explains how LncRNA sngh3 may promote hepatic steatosis. Multiple molecular approaches have been employed to identify molecular targets of the proposed mechanism, which is a strength of the study. There are, however, several potential issues to consider before jumping to a conclusion.

(1) First of all, it's important to ensure the robustness and rigor of each study. The manuscript was not carefully put together. The image qualities for several figures were poor, making it difficult for the readers to evaluate the results with confidence. The biological replicates and numbers of experimental repeats for cell-based assays were not described. When possible, the entire immunoblot imaging used for quantification should be presented (rather than showing n=1 representative). There were multiple mislabels in figure panels or figure legends (e.g., Figure 2I, Figure 2K, and Figure 3K). The b-actin immunoblot image was reused in Figure 4J, Figure 5G, and Figure 7B with different exposure times. These might be from the same cohort of mice. If the immunoblots were run at different times, the loading control should be included on the same blot as well.

We thank the reviewer for the detailed comment. We have provided the clear figures in revised manuscript, please check them.

The biological replicates and numbers of experimental repeats for cell-based assays had been updated and please check them in the manuscript.

The entire immunoblot imaging used for quantification had been provided in the primary data. Please check them.

The original Figure 2I, Figure 2K, Figure 3K have been revised and replaced with new Figure 2F, Figure 2H, Figure 3H, and their corresponding figure legends has also been corrected in revised manuscript.

The protein levels of CD36, PPARγ and β-ACTIN were examined at the same time and we had revised the manuscript, please check them in revised Figure 7B and 7C.

(2) The authors can do a better job in explaining the logic for how they came up with the potential function of each component of the signaling cascade. Snhg3 is down-regulated by HFD. However, the evidence presented indicates its involvement in promoting steatosis. In Figure 1C, one would expect PPARg expression to be up-regulated (when Sngh3 was down-regulated). If so, the physiological observation conflicts with the proposed mechanism. In addition, SND1 is known to regulate RNA/miRNA processing. How do the authors rule out this potential mechanism? How about the hosting snoRNA, Snord17? Does it involve the progression of NASLD?

We thank the reviewer for the detailed comment. Our results showed that the expression of Snhg3 was decreased in DIO mice which led us to speculate that the downregulation of Snhg3 in DIO mice might be a stress protective reaction to high nutritional state, but the specific details need to be clarified. This is probably similar to fibroblast growth factor 21 (FGF21) and growth differentiation factor 15 (GDF15), whose endogenous expression and circulating levels are elevated in obese humans and mice despite their beneficial effects on obesity and related metabolic complications (Keipert and Ost, 2021). Although FGF21 can be induced by oxidative stress and be activated in obese mice and in NASH patients, elevated FGF21 paradoxically protects against oxidative stress and reduces hepatic steatosis (Tillman and Rolph, 2020).  We had added the content the section of Discussion, please check it in the second paragraph in p12.

SND1 has multiple roles through associating with different types of RNA molecules, including mRNA, miRNA, circRNA, dsRNA and lncRNA. SND1 could bind negative-sense SARS-CoV-2 RNA and promoted viral RNA synthesis, and to promote viral RNA synthesis (Schmidt et al., 2023). SND1 is also involved in hypoxia by negatively regulating hypoxia‐related miRNAs (Saarikettu et al., 2023). Furthermore, a recent study revealed that lncRNA SNAI3-AS1 can competitively bind to SND1 and perturb the m6A-dependent recognition of Nrf2 mRNA 3'UTR by SND1, thereby reducing the mRNA stability of Nrf2 (Zheng et al., 2023). Huang et al. also reported that circMETTL9 can directly bind to and increase the expression of SND1 in astrocytes, leading to enhanced neuroinflammation (Huang et al., 2023). However, whether there is an independent-histone methylation role of SND1/lncRNA-Snhg3 involved in lipid metabolism in the liver needs to be further investigated. We also discussed the limitation in the manuscript and please refer the section of Discussion in the third paragraph in p17.

Snhg3 serves as host gene for producing intronic U17 snoRNAs, the H/ACA snoRNA. A previous study found that cholesterol trafficking phenotype was not due to reduced Snhg3 expression, but rather to haploinsufficiency of U17 snoRNA. Upregulation of hypoxia-upregulated mitochondrial movement regulator (HUMMR) in U17 snoRNA-deficient cells promoted the formation of ER-mitochondrial contacts, resulting in decreasing cholesterol esterification and facilitating cholesterol trafficking to mitochondria (Jinn et al., 2015). Additionally, disruption of U17 snoRNA caused resistance to lipid-induced cell death and general oxidative stress in cultured cells. Furthermore, knockdown of U17 snoRNA in vivo protected against hepatic steatosis and lipid-induced oxidative stress and inflammation (Sletten et al., 2021). We determined the expression of hepatic U17 snoRNA and its effect on SND1 and PPARγ. The results showed that the expression of U17 snoRNA decreased in the liver of DIO Snhg3-HKO mice and unchanged in the liver of DIO Snhg3-HKI mice, but overexpression of U17 snoRNA had no effect on the expression of SND1 and PPARγ (figure supplement 5A-C), indicating that Sngh3 induced hepatic steatosis was independent on U17 snoRNA. We also discussed it in revised manuscript, please refer the section of Discussion in p15.

References

HUANG, C., SUN, L., XIAO, C., YOU, W., SUN, L., WANG, S., ZHANG, Z. & LIU, S. 2023. Circular RNA METTL9 contributes to neuroinflammation following traumatic brain injury by complexing with astrocytic SND1. J Neuroinflammation, 20, 39. DIO:10.1186/s12974-023-02716-x, PMID:36803376

JINN, S., BRANDIS, K. A., REN, A., CHACKO, A., DUDLEY-RUCKER, N., GALE, S. E., SIDHU, R., FUJIWARA, H., JIANG, H., OLSEN, B. N., SCHAFFER, J. E. & ORY, D. S. 2015. snoRNA U17 regulates cellular cholesterol trafficking. Cell Metab, 21, 855-67. DIO:10.1016/j.cmet.2015.04.010, PMID:25980348

KEIPERT, S. & OST, M. 2021. Stress-induced FGF21 and GDF15 in obesity and obesity resistance. Trends Endocrinol Metab, 32, 904-915. DIO:10.1016/j.tem.2021.08.008, PMID:34526227

SAARIKETTU, J., LEHMUSVAARA, S., PESU, M., JUNTTILA, I., PARTANEN, J., SIPILA, P., POUTANEN, M., YANG, J., HAIKARAINEN, T. & SILVENNOINEN, O. 2023. The RNA-binding protein Snd1/Tudor-SN regulates hypoxia-responsive gene expression. FASEB Bioadv, 5, 183-198. DIO:10.1096/fba.2022-00115, PMID:37151849

SCHMIDT, N., GANSKIH, S., WEI, Y., GABEL, A., ZIELINSKI, S., KESHISHIAN, H., LAREAU, C. A., ZIMMERMANN, L., MAKROCZYOVA, J., PEARCE, C., KREY, K., HENNIG, T., STEGMAIER, S., MOYON, L., HORLACHER, M., WERNER, S., AYDIN, J., OLGUIN-NAVA, M., POTABATTULA, R., KIBE, A., DOLKEN, L., SMYTH, R. P., CALISKAN, N., MARSICO, A., KREMPL, C., BODEM, J., PICHLMAIR, A., CARR, S. A., CHLANDA, P., ERHARD, F. & MUNSCHAUER, M. 2023. SND1 binds SARS-CoV-2 negative-sense RNA and promotes viral RNA synthesis through NSP9. Cell, 186, 4834-4850 e23. DIO:10.1016/j.cell.2023.09.002, PMID:37794589

SLETTEN, A. C., DAVIDSON, J. W., YAGABASAN, B., MOORES, S., SCHWAIGER-HABER, M., FUJIWARA, H., GALE, S., JIANG, X., SIDHU, R., GELMAN, S. J., ZHAO, S., PATTI, G. J., ORY, D. S. & SCHAFFER, J. E. 2021. Loss of SNORA73 reprograms cellular metabolism and protects against steatohepatitis. Nat Commun, 12, 5214. DIO:10.1038/s41467-021-25457-y, PMID:34471131

TILLMAN, E. J. & ROLPH, T. 2020. FGF21: An Emerging Therapeutic Target for Non-Alcoholic Steatohepatitis and Related Metabolic Diseases. Front Endocrinol (Lausanne), 11, 601290. DIO:10.3389/fendo.2020.601290, PMID:33381084

ZHENG, J., ZHANG, Q., ZHAO, Z., QIU, Y., ZHOU, Y., WU, Z., JIANG, C., WANG, X. & JIANG, X. 2023. Epigenetically silenced lncRNA SNAI3-AS1 promotes ferroptosis in glioma via perturbing the m(6)A-dependent recognition of Nrf2 mRNA mediated by SND1. J Exp Clin Cancer Res, 42, 127. DIO:10.1186/s13046-023-02684-3, PMID:37202791

(3) The role of PPARg in fatty liver diseases might be a rodent-specific phenomenon. PPARg agonist treatment in humans may actually reduce ectopic fat deposition by increasing fat storage in adipose tissues. The relevance of the findings to human diseases should be discussed.

We thank the reviewer for the detailed comment. As a transcription regulator of Cd36 and Cidea/c, it is well known that PPARγ plays major adipogenic and lipogenic roles in adipose tissue. Although the expression of PPARγ in the liver is very low under healthy conditions, induced expression of PPARγ in both hepatocytes and non-parenchymal cells (Kupffer cells, immune cells, and hepatic stellate cells (HSCs)) in the liver has a crucial role in the pathophysiology of MASLD (Lee et al., 2023b, Chen et al., 2023, Gross et al., 2017). The activation of PPARγ in the liver induces the adipogenic program to store fatty acids in lipid droplets as observed in adipocytes (Lee et al., 2018). Moreover, the inactivation of liver PPARγ abolished rosiglitazone-induced an increase in hepatic TG and improved hepatic steatosis in lipoatrophic AZIP mice (Gavrilova et al., 2003). Apart from promoting lipogenesis, PPARγ has also a crucial function in improving inflammation and fibrosis (Chen et al., 2023). Furthermore, there is a strong correlation between the onset of hepatic steatosis and hepatocyte-specific PPARγ expression. Clinical trials have also indicated that increased insulin resistance and hepatic PPARγ expressions were associated with NASH scores in some obese patients (Lee et al., 2023a, Mukherjee et al., 2022). Even though PPARγ’s primary function is in adipose tissue, patients with MASLD have much higher hepatic expression levels of PPARγ, reflecting the fact that PPARγ plays different roles in different tissues and cell types (Mukherjee et al., 2022). As these studies mentioned above, our result also hinted at the importance of PPARγ in the pathophysiology of MASLD. Snhg3 deficiency or overexpression respectively induced the decrease or increase in hepatic PPARγ. Moreover, administration of PPARγ antagonist T0070907 mitigated the hepatic Cd36 and Cidea/c increase and improved Snhg3-induced hepatic steatosis. However,  conflicting findings suggest that the expression of hepatic PPARγ is not increased as steatosis develops in humans and in clinical studies and that PPARγ agonists administration didn’t aggravate liver steatosis (Gross et al., 2017). Thus, understanding how the hepatic PPARγ expression is regulated may provide a new avenue to prevent and treat the MASLD (Lee et al., 2018). We also discussed it in revised manuscript, please refer the first paragraph in the section of Discussion in p13.

References

CHEN, H., TAN, H., WAN, J., ZENG, Y., WANG, J., WANG, H. & LU, X. 2023. PPAR-gamma signaling in nonalcoholic fatty liver disease: Pathogenesis and therapeutic targets. Pharmacol Ther, 245, 108391. DIO:10.1016/j.pharmthera.2023.108391, PMID:36963510

GAVRILOVA, O., HALUZIK, M., MATSUSUE, K., CUTSON, J. J., JOHNSON, L., DIETZ, K. R., NICOL, C. J., VINSON, C., GONZALEZ, F. J. & REITMAN, M. L. 2003. Liver peroxisome proliferator-activated receptor gamma contributes to hepatic steatosis, triglyceride clearance, and regulation of body fat mass. J Biol Chem, 278, 34268-76. DIO:10.1074/jbc.M300043200, PMID:12805374

GROSS, B., PAWLAK, M., LEFEBVRE, P. & STAELS, B. 2017. PPARs in obesity-induced T2DM, dyslipidaemia and NAFLD. Nat Rev Endocrinol, 13, 36-49. DIO:10.1038/nrendo.2016.135, PMID:27636730

LEE, S. M., MURATALLA, J., KARIMI, S., DIAZ-RUIZ, A., FRUTOS, M. D., GUZMAN, G., RAMOS-MOLINA, B. & CORDOBA-CHACON, J. 2023a. Hepatocyte PPARgamma contributes to the progression of non-alcoholic steatohepatitis in male and female obese mice. Cell Mol Life Sci, 80, 39. DIO:10.1007/s00018-022-04629-z, PMID:36629912

LEE, S. M., MURATALLA, J., SIERRA-CRUZ, M. & CORDOBA-CHACON, J. 2023b. Role of hepatic peroxisome proliferator-activated receptor gamma in non-alcoholic fatty liver disease. J Endocrinol, 257. DIO:10.1530/JOE-22-0155, PMID:36688873

LEE, Y. K., PARK, J. E., LEE, M. & HARDWICK, J. P. 2018. Hepatic lipid homeostasis by peroxisome proliferator-activated receptor gamma 2. Liver Res, 2, 209-215. DIO:10.1016/j.livres.2018.12.001, PMID:31245168

MUKHERJEE, A. G., WANJARI, U. R., GOPALAKRISHNAN, A. V., KATTURAJAN, R., KANNAMPUZHA, S., MURALI, R., NAMACHIVAYAM, A., GANESAN, R., RENU, K., DEY, A., VELLINGIRI, B. & PRINCE, S. E. 2022. Exploring the Regulatory Role of ncRNA in NAFLD: A Particular Focus on PPARs. Cells, 11. DIO:10.3390/cells11243959, PMID:36552725

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

As a general strategy for the revision, I would advise the authors to focus on strengthening the analysis of the liver with the two most important figures being Figure 2 and Figure 3. The mechanism as it stands is problematic which reduces the impact of the animal studies despite substantial efforts from the authors. Consider removing or toning down some of the studies focused on mechanisms in the nucleus, including changing the title.

We thank the reviewer for the detailed comment. In this study, hepatocyte-specific Snhg3 deficiency decreased body and liver weight, alleviated hepatic steatosis and promoted hepatic fatty acid metabolism in DIO mice, whereas overexpression induced the opposite effect. The hepatic differentially expressed genes (DEGs) between the DIO Snhg3-HKI and control WT mice using RNA-Seq and revealed that Snhg3 exerts a global effect on the expression of genes involved in fatty acid metabolism using GSEA (Figure 4B). RT-qPCR analysis confirmed that the hepatic expression levels of some genes involved in fatty acid metabolism, including Cd36, Cidea/c and Scd1/2, were upregulated in Snhg3-HKO mice and were downregulated in Snhg3-HKI mice compared to the controls (Figure 4C). Moreover, deficiency and overexpression of Snhg3 respectively decreased and increased the expression of profibrotic genes, such as Col1a1 and Col1a2, but had no effects on the pro-inflammatory factors, including Tgfβ1, Tnfα, Il6 and Il1β (figure supplement 3A and B). The results indicated that Snhg3 involved in hepatic steatosis through regulating fatty acid metabolism. Furthermore, PPARγ was selected to study its role in Snhg3-induced hepatic steatosis by integrated analyzing the data from CUT&Tag-Seq, ATAC-Seq and RNA-Seq. Finally, inhibition of PPARγ with T0070907 alleviated Snhg3 induced Cd36 and Cidea/c increases and improved Snhg3-aggravated hepatic steatosis. In summary, we confirmed that SND1/H3K27me3/PPARγ is partially responsible for Sngh3-inuced hepatic steatosis. As the reviewer suggested, we replaced the title with “LncRNA-Snhg3 Aggravates Hepatic Steatosis via PPARγ Signaling”.

(1) How is steatosis changing in the liver? Is this due to a change in fatty acid uptake, lipogenesis/synthesis, beta-oxidation, trig secretion, etc..? The analysis in Figures 2 and 3 is mostly focused on metabolic chamber studies which seem distracting, particularly in the absence of a mechanism and given a liver-specific perturbation. The authors should use a combination of targeted gene expression, protein blots, and lipid flux measurements to provide better insights here. The histology in Figure 2H suggests a very dramatic effect but does match with lipid measurements in 2I.

We thank the reviewer for the detailed comment. The pathogenesis of MASLD has not been entirely elucidated. Multifarious factors such as genetic and epigenetic factors, nutritional factors, insulin resistance, lipotoxicity, microbiome, fibrogenesis and hormones secreted from the adipose tissue, are recognized to be involved in the development and progression of MASLD (Buzzetti et al., 2016, Lee et al., 2017, Rada et al., 2020, Sakurai et al., 2021, Friedman et al., 2018). In this study, we investigated the hepatic differentially expressed genes (DEGs) between the DIO Snhg3-HKI and control WT mice using RNA-Seq and revealed that Snhg3 exerts a global effect on the expression of genes involved in fatty acid metabolism using GSEA (Figure 4B). We validated the expression of some DEGs involved in fatty acid metabolism by RT-qPCR. The results showed that the hepatic expression levels of some genes involved in fatty acid metabolism, including Cd36, Cidea/c and Scd1/2 were upregulated in Snhg3-HKO mice and were downregulated in Snhg3-HKI mice compared to the controls (Figure 4C), respectively. Additionally, we re-analyzed the metabolic chamber data using CalR and the results showed that there were no obvious differences in heat production, total oxygen consumption, carbon dioxide production or RER between DIO Snhg3-HKO or DIO Snhg3-HKI and the corresponding control mice (figure supplement 1C and 2C). Unfortunately, we did not detect lipid flux due to limited experimental conditions. However, in summary, our results indicated that Snhg3 is involved in hepatic steatosis by regulating fatty acid metabolism. Please check them in the first paragraph in p8.

Additionally, we determined the hepatic TC levels in other batch of DIO Snhg3-HKO and control mice and found there was no difference in hepatic TC (as below) between DIO Snhg3-HKO and control mice fed HFD 18 weeks. Perhaps the apparent difference in TC requires a prolonged high-fat diet feeding time.

Author response image 1.

Hepatic TC contents of in DIO Snhg3-Flox and Snhg3-HKO mice.

References

BUZZETTI, E., PINZANI, M. & TSOCHATZIS, E. A. 2016. The multiple-hit pathogenesis of non-alcoholic fatty liver disease (NAFLD). Metabolism, 65, 1038-48. DIO:10.1016/j.metabol.2015.12.012, PMID:26823198

FRIEDMAN, S. L., NEUSCHWANDER-TETRI, B. A., RINELLA, M. & SANYAL, A. J. 2018. Mechanisms of NAFLD development and therapeutic strategies. Nat Med, 24, 908-922. DIO:10.1038/s41591-018-0104-9, PMID:29967350

LEE, J., KIM, Y., FRISO, S. & CHOI, S. W. 2017. Epigenetics in non-alcoholic fatty liver disease. Mol Aspects Med, 54, 78-88. DIO:10.1016/j.mam.2016.11.008, PMID:27889327

RADA, P., GONZALEZ-RODRIGUEZ, A., GARCIA-MONZON, C. & VALVERDE, A. M. 2020. Understanding lipotoxicity in NAFLD pathogenesis: is CD36 a key driver? Cell Death Dis, 11, 802. DIO:10.1038/s41419-020-03003-w, PMID:32978374

SAKURAI, Y., KUBOTA, N., YAMAUCHI, T. & KADOWAKI, T. 2021. Role of Insulin Resistance in MAFLD. Int J Mol Sci, 22. DIO:10.3390/ijms22084156, PMID:33923817

(2) Throughout the manuscript the authors make claims about liver disease models, but this is not well supported since markers of advanced liver disease are not examined. The authors should stain and show expression for fibrosis and inflammation.

We thank the reviewer for the detailed comment. Metabolic dysfunction-associated fatty liver disease (MASLD) is characterized by excess liver fat in the absence of significant alcohol consumption. It can progress from simple steatosis to metabolic dysfunction-associated steatohepatitis (MASH) and fibrosis and eventually to chronic progressive diseases such as cirrhosis, end-stage liver failure, and hepatocellular carcinoma (Loomba et al., 2021). As the reviewer suggested, we detected the effect of Snhg3 on liver fibrosis and inflammation. The results showed no hepatic fibrosis phenotype was seen in Snhg3-HKO and Snhg3-HKI mice (figures supplement 1D and 2D). Moreover, deficiency and overexpression of Snhg3 respectively decreased and increased the expression of profibrotic genes, such as collagen type I alpha 1/2 (Col1a1 and Col1a2), but had no effects on the pro-inflammatory factors including Tgf-β, Tnf-α, Il-6 and Il-1β (figure supplement 3A and 3B). Inflammation is an absolute requirement for fibrosis because factors from injured hepatocytes alone are not sufficient to directly activate HSCs and lead to fibrosis (Kisseleva and Brenner, 2021). Additionally, previous studies indicated that exposure to HFD for more 24 weeks causes less severe fibrosis (Alshawsh et al., 2022). In future, the effect of Snhg3 on hepatic fibrosis in mice need to be elucidated by prolonged high-fat feeding or by adopting methionine- and choline deficient diet (MCD) feeding. Please check them in the second paragraph in the section of Discussion in p13.

References

ALSHAWSH, M. A., ALSALAHI, A., ALSHEHADE, S. A., SAGHIR, S. A. M., AHMEDA, A. F., AL ZARZOUR, R. H. & MAHMOUD, A. M. 2022. A Comparison of the Gene Expression Profiles of Non-Alcoholic Fatty Liver Disease between Animal Models of a High-Fat Diet and Methionine-Choline-Deficient Diet. Molecules, 27. DIO:10.3390/molecules27030858, PMID:35164140

KISSELEVA, T. & BRENNER, D. 2021. Molecular and cellular mechanisms of liver fibrosis and its regression. Nat Rev Gastroenterol Hepatol, 18, 151-166. DIO:10.1038/s41575-020-00372-7, PMID:33128017

LOOMBA, R., FRIEDMAN, S. L. & SHULMAN, G. I. 2021. Mechanisms and disease consequences of nonalcoholic fatty liver disease. Cell, 184, 2537-2564. DIO:10.1016/j.cell.2021.04.015, PMID:33989548

(3) Publicly available datasets show that PPARG protein is not expressed in the liver (Science 2015 347(6220):1260419, PMID: 25613900). Are the authors sure this is not an effect on another PPAR isoform like alpha? ChIP and RNA-seq pathway readouts do not distinguish between different isoforms.

We thank the reviewer for the detailed comment. As a transcription regulator of Cd36 and Cidea/c, it is well known that PPARγ plays major adipogenic and lipogenic roles in adipose tissue. Although the expression of PPARγ in the liver is very low under healthy conditions, induced expression of PPARγ in both hepatocytes and non-parenchymal cells (Kupffer cells, immune cells, and hepatic stellate cells (HSCs)) in the liver has a crucial role in the pathophysiology of MASLD (Lee et al., 2023b, Chen et al., 2023, Gross et al., 2017). The activation of PPARγ in the liver induces the adipogenic program to store fatty acids in lipid droplets as observed in adipocytes (Lee et al., 2018). Moreover, the inactivation of liver PPARγ abolished rosiglitazone-induced an increase in hepatic TG and improved hepatic steatosis in lipoatrophic AZIP mice (Gavrilova et al., 2003). Apart from promoting lipogenesis, PPARγ has also a crucial function in improving inflammation and fibrosis (Chen et al., 2023). Furthermore, there is a strong correlation between the onset of hepatic steatosis and hepatocyte-specific PPARγ expression. Clinical trials have also indicated that increased insulin resistance and hepatic PPARγ expressions were associated with NASH scores in some obese patients (Lee et al., 2023a, Mukherjee et al., 2022). Even though PPARγ’s primary function is in adipose tissue, patients with MASLD have much higher hepatic expression levels of PPARγ, reflecting the fact that PPARγ plays different roles in different tissues and cell types (Mukherjee et al., 2022). As these studies mentioned above, our result also hinted at the importance of PPARγ in the pathophysiology of MASLD. Snhg3 deficiency or overexpression respectively induced the decrease or increase in hepatic PPARγ. Moreover, administration of PPARγ antagonist T0070907 mitigated the hepatic Cd36 and Cidea/c increase and improved Snhg3-induced hepatic steatosis. However,  conflicting findings suggest that the expression of hepatic PPARγ is not increased as steatosis develops in humans and in clinical studies and that PPARγ agonists administration didn’t aggravate liver steatosis (Gross et al., 2017). Thus, understanding how the hepatic PPARγ expression is regulated may provide a new avenue to prevent and treat the MASLD (Lee et al., 2018). We also discussed it in revised manuscript, please refer the first paragraph in the section of Discussion in p13 in revised manuscript.

PPARα, most highly expressed in the liver, transcriptionally regulates lipid catabolism by regulating the expression of genes mediating triglyceride hydrolysis, fatty acid transport, and β-oxidation. Activators of PPARα decrease plasma triglycerides by inhibiting its synthesis and accelerating its hydrolysis (Chen et al., 2023). Mice with deletion of the Pparα gene exhibited more hepatic steatosis under HFD induction. As the reviewer suggested, we investigated the effect of Snhg3 on Pparα expression.  The result showed that both deficiency of Snhg3 or overexpression of Snhg3 doesn’t affect the mRNA level of Pparα as showing below, indicating that Snhg3-induced lipid accumulation independent on PPARα. Additionally, the exon, upstream 2k, 5’-UTR and intron regions of Pparγ, not Pparα, were enriched with the H3K27me3 mark (fold_enrichment = 4.15697) in the liver of DIO Snhg3-HKO mice using the CUT&Tag assay (table supplement 8), which was further confirmed by ChIP (Figure 6F and G). Therefore, we choose PPARγ to study its role in Sngh3-induced hepatic steatosis by integrated analyzing the data from CUT&Tag-Seq, ATAC-Seq and RNA-Seq.

Author response image 2.

The mRNA levels of hepatic Pparα expression in DIO Snhg3-HKO mice and Snhg3-HKI mice compared to the controls.

References

CHEN, H., TAN, H., WAN, J., ZENG, Y., WANG, J., WANG, H. & LU, X. 2023. PPAR-gamma signaling in nonalcoholic fatty liver disease: Pathogenesis and therapeutic targets. Pharmacol Ther, 245, 108391. DIO:10.1016/j.pharmthera.2023.108391, PMID:36963510

GAVRILOVA, O., HALUZIK, M., MATSUSUE, K., CUTSON, J. J., JOHNSON, L., DIETZ, K. R., NICOL, C. J., VINSON, C., GONZALEZ, F. J. & REITMAN, M. L. 2003. Liver peroxisome proliferator-activated receptor gamma contributes to hepatic steatosis, triglyceride clearance, and regulation of body fat mass. J Biol Chem, 278, 34268-76. DIO:10.1074/jbc.M300043200, PMID:12805374

GROSS, B., PAWLAK, M., LEFEBVRE, P. & STAELS, B. 2017. PPARs in obesity-induced T2DM, dyslipidaemia and NAFLD. Nat Rev Endocrinol, 13, 36-49. DIO:10.1038/nrendo.2016.135, PMID:27636730

LEE, S. M., MURATALLA, J., KARIMI, S., DIAZ-RUIZ, A., FRUTOS, M. D., GUZMAN, G., RAMOS-MOLINA, B. & CORDOBA-CHACON, J. 2023a. Hepatocyte PPARgamma contributes to the progression of non-alcoholic steatohepatitis in male and female obese mice. Cell Mol Life Sci, 80, 39. DIO:10.1007/s00018-022-04629-z, PMID:36629912

LEE, S. M., MURATALLA, J., SIERRA-CRUZ, M. & CORDOBA-CHACON, J. 2023b. Role of hepatic peroxisome proliferator-activated receptor gamma in non-alcoholic fatty liver disease. J Endocrinol, 257. DIO:10.1530/JOE-22-0155, PMID:36688873

LEE, Y. K., PARK, J. E., LEE, M. & HARDWICK, J. P. 2018. Hepatic lipid homeostasis by peroxisome proliferator-activated receptor gamma 2. Liver Res, 2, 209-215. DIO:10.1016/j.livres.2018.12.001, PMID:31245168

MUKHERJEE, A. G., WANJARI, U. R., GOPALAKRISHNAN, A. V., KATTURAJAN, R., KANNAMPUZHA, S., MURALI, R., NAMACHIVAYAM, A., GANESAN, R., RENU, K., DEY, A., VELLINGIRI, B. & PRINCE, S. E. 2022. Exploring the Regulatory Role of ncRNA in NAFLD: A Particular Focus on PPARs. Cells, 11. DIO:10.3390/cells11243959, PMID:36552725

(4) Previous work suggests that SNHG3 regulates its neighboring gene MED18 which is an important regulator of global transcription. Could some of the observed effects be due to changes in MED18 or other neighboring genes?

We thank the reviewer for the detailed comment. Previous work suggested that human SNHG3 promotes progression of gastric cancer by regulating neighboring MED18 gene methylation (Xuan and Wang, 2019). Here, we studied the effect of mouse Snhg3 on Med18 and the result showed that Snhg3 had no effect on the mRNA levels of Med18 (as below). Additionally, we also tested the effect of mouse Snhg3 on its neighboring gene, regulator of chromosome condensation 1 (Rcc1). Although deficiency of Snhg3 inhibited the mRNA level of Rcc1, overexpression of Snhg3 doesn’t affect the mRNA level of Rcc1 as showing below. RCC1, the only known guanine nucleotide exchange factor in the nucleus for Ran, a nuclear Ras-like G protein, directly participates in cellular processes such as nuclear envelope formation, nucleocytoplasmic transport, and spindle formation (Ren et al., 2020). RCC1 also regulates chromatin condensation in the late S and early M phases of the cell cycle. Many studies have found that RCC1 plays an important role in tumors. Furthermore, whether Rcc1 mediates the alleviated effect on MASLD of Snhg3 needs to be further investigated.

Author response image 3.

The mRNA levels of hepatic Rcc1 and Med18 expression in DIO Snhg3-HKO mice and Snhg3-HKI mice compared to the controls.

References

REN, X., JIANG, K. & ZHANG, F. 2020. The Multifaceted Roles of RCC1 in Tumorigenesis. Front Mol Biosci, 7, 225. DIO:10.3389/fmolb.2020.00225, PMID:33102517

XUAN, Y. & WANG, Y. 2019. Long non-coding RNA SNHG3 promotes progression of gastric cancer by regulating neighboring MED18 gene methylation. Cell Death Dis, 10, 694. DIO:10.1038/s41419-019-1940-3, PMID:31534128

(5) The claim that Snhg3 regulates SND1 protein stability seems subtle. There is data inconsistency between different panels regarding this regulation including Figure 5I, Figure 6A, and Figure 7E. In addition, is ubiquitination happening in the nucleus where Snhg3 is expressed?

We thank the reviewer for the detailed comment. The effect of Snhg3-induced SND1 expression had been confirmed by western blotting, please check them in Figure 5I, Figure 6A, Figure 7E and corresponding primary data. Additionally, Snhg3-induced SND1 protein stability seemed subtle, indicating there may be other mechanism by which Snhg3 promotes SND1, such as riboregulation. We had added it in the section of Discussion, please check it in the second paragraph in p16.

Additionally, we did not detect the sites where SND1 is modified by ubiquitination. Our results showed that Snhg3 was more localized in the nucleus (Figure 1D) and Snhg3 also promoted the nuclear localization of SND1 (Figure 5O). We had revised the diagram of Snhg3 action in Figure 8G. Please check them in revised manuscript.

(6) The authors show that the loss of Snhg3 changes the global H3K27me3 level. Few enzymes modify H3K27me3 levels. Did the authors check for an interaction between EZH2, Jmjd3, UTX, and Snhg3/SND1?

We thank the reviewer for the detailed comment. It is crucial to ascertain whether SND1 itself functions as a new demethylase or if it influences other demethylases, such as Jmjd3, enhancer of zeste homolog 2 (EZH2), and ubiquitously transcribed tetratricopeptide repeat on chromosome X (UTX). The precise mechanism by which SND1 regulates H3K27me3 is still unclear and hence requires further investigation. We had added the limitations in the section of Discussion and please check it in the third paragraph in p17.

(7) Can the authors speculate if the findings related to Snhg3/SND1 extend to humans?

We thank the reviewer for the detailed comment. Since the sequence of Snhg3 is not conserved between mice and humans, the findings in this manuscript may not be applicable to humans, but the detail need to be further exploited.

(8) As a general rule the figures are too small or difficult to read with limited details in the figure legends which limits evaluation. For example, Figure 1B and almost all of 4 cannot read labels. Figure 2, cannot see the snapshots show of mice or livers. What figure is supporting the claim that snhg3KI are more 'hyper-accessible'? Can the authors clarify what Figure 4H is referring to?

We thank the reviewer for the detailed comment. We have provided high quality figures in our revised manuscript.

The ‘hyper-accessible’ state in the liver of Snhg3-HKI mice was inferred by the differentially accessible regions (DARs), that is, we discovered 4305 DARs were more accessible in Snhg3-HKI mice and only 2505 DARs were more accessible in control mice and please refer table supplement 3).

The result of Figure 4H about heatmap for Cd36 was from hepatic RNA-seq of DIO Snhg3-HKI and control WT mice. For avoiding ambiguity, we have removed it.

(9) Authors stated that upon Snhg3 knock out, more genes are upregulated(1028) than downregulated(365). This description does not match Figure 4A. It seems in Figure 4A there are equal numbers of up and downregulated genes.

We thank the reviewer for the detailed question. We apologized for this mistake and have corrected it.

(10) Provide a schematic of the knockout and KI strategy in the supplement.

We thank the reviewer for the detailed comment. We had included the knockout and KI strategy in figure supplement 1A and B, and 2A.

Reviewer #2 (Recommendations For The Authors):

(1) Metabolic cage data need to be reanalyzed with CalR (particularly when the body weights are significantly different).

We thank the reviewer for the detailed comment. We reanalyzed the metabolic cage data using CalR (Mina et al., 2018). The results showed that there were no obvious differences in heat production, total oxygen consumption, carbon dioxide production and the respiratory exchange ratio between DIO Snhg3-HKO and control mice. Similar to DIO Snhg3-HKO mice, there was also no differences in heat production, total oxygen consumption, carbon dioxide production, and RER between DIO Snhg3-HKI mice and WT mice. Please check them in figure supplement 1C and 2C, and Mouse Calorimetry in Materials and Methods.

Reference

MINA, A. I., LECLAIR, R. A., LECLAIR, K. B., COHEN, D. E., LANTIER, L. & BANKS, A. S. 2018. CalR: A Web-Based Analysis Tool for Indirect Calorimetry Experiments. Cell Metab, 28, 656-666 e1. DIO:10.1016/j.cmet.2018.06.019, PMID:30017358

(2) ITT in Figure 2F should also be presented as % of the initial glucose level, which would reveal that there is no difference between WT and KO.

We thank the reviewer for the detailed comment. We repeated ITT experiment and include the new data in revised manuscript, please check it in Figure 2C.

(3) The fasting glucose results are inconsistent between ITT and GTT. Is there any difference in fasting glucose?

We thank the reviewer for the questions. The difference between GTT and ITT was caused owing to different fasting time, that is, mice were fasted for 6 h in ITT and were fasted for 16 h in GTT. It seems that Snhg3 doesn’t affect short- and longer-time fasting glucose levels and please refer Figures 2C and 3C.

Author response:

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

Weaknesses Reviewer 1: 

There are a number of weaknesses in the study. The small sample size is a significant limitation of the study. Out of 31 patients, only 17 patients were reported to develop neuropathy, with significant neuropathy (grade 2/3) in only 5 patients. The authors acknowledge this limitation in the results and discussion sections of the manuscript, but it limits the interpretation of the results. Also acknowledged is the limited method used to assess neuropathy. 

We agree with the reviewer that the cohort size and assessment of neuropathy are limitations of our study as we already described in the corresponding section of the manuscript. However, occurrence and grade of the neuropathy are in line with results reported from previous studies. From these studies, the expected occurrence of neuropathy with our therapeutic regimen is around 50-70% (54.9% in our cohort), and most patients (80-90%) are expected to experience Grade 1 neuropathy after 12 weeks (13). In these studies, neuropathy is assessed by using questionnaires or by grading via NCTCTCAE as in our study. In summary, assessment and occurrence of neuropathy of our reported cohort are in line with previous reports.

Potentially due to this small number of patients with neuropathy, the machine learning algorithms could not distinguish between samples with and without neuropathy. Only selected univariate analyses identified differences in lipid profiles potentially related to neuropathy.  

The data analysis consistently followed a "mixture of experts" approach, as this seems to be the most successful way to deal with omics data. We have elaborated on this in the Methods section, including several supporting references. Regarding the quoted sentence from the results section, after rereading it, we realized that it was somewhat awkwardly worded. What we mean is now better worded in the results section, namely “Although the three algorithms detected neuropathy in new cases, unseen during training, at balanced accuracy of up to 0.75, while only the guess level of 0.5 was achieved when using permuted data for training, the 95% CI of the performance measures was not separated from guess level”. Therefore, multivariate feature selection was not considered a valid approach, since it requires that the algorithms from which the feature importance is read can successfully perform their task of class assignment (4). Therefore, univariate methods (Cohen's d, FPR, FWE) were preferred, as well as a direct hypothesis transfer of the top hits from the abovementioned day1/2 assessments to neuropathy. Classical statistics consisting of direct group comparisons using Kruskal-Wallis tests (5) were performed.” 

It was our approach to investigate the data set in an unbiased manner by different machine learning algorithms and select those lipids that the majority of the algorithms considered important for distinguishing the patient groups (majority voting). This way, the inconsistencies and limitations of a single evaluation method, such as regression analysis, that occur in some datasets, can be mitigated. 

Three sphingolipid mediators including SA1P differed between patients with and without neuropathy at the end of treatment. These sphingolipids were elevated at the end of treatment in the cohort with neuropathy, relative to those without neuropathy. However, across all samples from pre to post-paclitaxel treatment, there was a significant reduction in SA1P levels. It is unclear from the data presented what the underlying mechanism for this result would be. 

We agree with the reviewer that our study does not identify the mechanism by which paclitaxel treatment alters sphingolipid concentrations in the plasma of patients. It has been reported before that paclitaxel may increase expression and activity of serine palmitoyltransferase (SPT) which is the crucial enzyme and rate-limiting step in the denovo synthesis of sphingolipids. This may be associated with a shift towards increased synthesis of 1-deoxysphingolipids and a decrease of “classical” sphingolipids (6) and may explain the general reduction of SA1P and other sphingolipid levels after paclitaxel treatment in our study. 

It is also conceivable that paclitaxel reduces the release of sphingolipids into the plasma. Paclitaxel is a microtubule stabilizing agent (7) that may interfere with intracellular transport processes and release of paracrine mediators. 

The mechanistic details of paclitaxel involvement in sphingolipid metabolism or transport are highly interesting but identifying them is beyond the scope of our manuscript.

If elevated SA1P is associated with neuropathy development, it would be expected to increase in those who develop neuropathy from pre to post-treatment time points. 

There is a general trend of reduced plasma SA1P concentrations following paclitaxel treatment. Nevertheless, patients experiencing neuropathy exhibit significantly elevated SA1P levels post-treatment. 

It has been shown before that paclitaxel-induced neuropathic pain requires activation of the S1P1 receptor in a preclinical study (8). Moreover, a meta-analysis of genome-wide association studies (GWAS) from two clinical cohorts identified multiple regulatory elements and increased activity of S1PR1 associated with paclitaxel-induced neuropathy (9). These data imply that enhanced S1P receptor activity and signaling are key drivers of paclitaxel-induced neuropathy. It seems that both, increased levels of the sphingolipid ligands in combination with enhanced expression and activity of S1P receptors can potentiate paclitaxel-induced neuropathy in patients. This explains why also decreased SA1P concentrations after paclitaxel treatment can still enhance neuropathy via the S1PRTRPV1 axis in sensory neurons.

We added this paragraph to the discussions section of our manuscript.

Primary sensory neuron cultures were used to examine the effects of SA1P application.

SA1P application produced calcium transients in a small proportion of sensory neurons. It is not clear how this experimental model assists in validating the role of SA1P in neuropathy development as there is no assessment of sensory neuron damage or other hallmarks of peripheral neuropathy. These results demonstrate that some sensory neurons respond to SA1P and that this activity is linked to TRPV1 receptors. However, further studies will be required to determine if this is mechanistically related to neuropathy.

As we detected elevated levels of SA1P in the plasma of PIPN patients, we can assume higher concentrations in the vicinity of sensory neurons. These neurons are the main drivers for neuropathy and neuropathic pain and are strongly affected by paclitaxel in their activity (10-15). Also, TRPV1 shows altered activity patterns in response to paclitaxel treatment (16). Because of its relevance for nociception and pathological pain, TRPV1 activity is a suitable and representative readout for pathological pain states in peripheral sensory neurons (17, 18), which is why we investigated them.

We would like to point out the potency of SA1P to increase capsaicin-induced calciumtransients in sensory neurons at submicromolar concentrations. 

We also agree with the reviewer that further studies need to investigate the underlying mechanisms in more detail. We added this sentence to the final paragraph in the discussion section of our manuscript.

Weaknesses Reviewer 2: 

The article is poorly written, hindering a clear understanding of core results. While the study's goals are apparent, the interpretation of sphingolipids, particularly SA1P, as key mediators of paclitaxel-induced neuropathy lacks robust evidence. 

We agree that the relevance of SA1P as key mediator of paclitaxel-induced neuropathy might be overstated and changed the wording throughout the manuscript accordingly. However, we would like to point out the potency of this lipid to increase capsaicin-induced calcium-transients in sensory neurons at submicromolar concentrations. 

Also, the lipid signature in the plasma of PIPN patients shows a unique pattern and sphingolipids are the group that showed the strongest alterations when comparing the patient groups. We also measured eicosanoids, such as prostaglandins, linoleic acid metabolites, endocannabinoids and other lipid groups that have previously been associated with influences on pain perception or nociceptor sensitization. However, none of these lipids showed significant differences in their concentrations in patient plasma. This is why we consider sphingolipids as contributors to or markers of paclitaxel-induced neuropathy in patients.

We also revised the entire article to improve its clarity.

The introduction fails to establish the significance of general neuropathy or peripheral neuropathy in anticancer drug-treated patients, and crucial details, such as the percentage of patients developing general neuropathy or peripheral neuropathy, are omitted. This omission is particularly relevant given that only around 50% of patients developed neuropathy in this study, primarily of mild Grade 1 severity with negligible symptoms, contradicting the study's assertion of CIPN as a significant side effect. 

As we already described in the introduction, CIPN is a serious dose- and therapy-limiting side effect, which affects up to 80% of treated patients. This depends on dose and combination of chemotherapeutic agents. For paclitaxel, therapeutic doses range from 80 – 225 mg/m². As CIPN symptoms are dose-dependent, the number of PIPN patients that receive a high paclitaxel dose is higher than the number of PIPN patient receiving a low dose.

In our study, we mainly used a low dose paclitaxel, because this therapeutic regimen is the most widely used paclitaxel monotherapy. From previous studies, the expected occurrence of neuropathy with this therapeutic regimen is around 50-70%, and most patients (8090%) are expected to experience Grade 1 neuropathy after 12 weeks (1-3).

Our results are within the range reported by these studies (54.9% patients with neuropathy). Also, as we highlight in Table S1, the neuropathy symptoms persist in most cases for several years after chemotherapy, affecting quality of life of these patients which makes it far from being a negligible symptom.

We added some more information concerning PIPN in the introduction section in which we emphasize the clinical problem.

The lack of clarity in distinguishing results obtained by lipidomics using machine learning methods and conventional methods adds to the confusion. The poorly written results section fails to specify SA1P's downregulation or upregulation, and the process of narrowing down to sphingolipids and SA1P is inadequately explained. 

We have tried to keep the machine learning part in the main manuscript short and moved major parts of it to a supplement. However, as this has been claimed to have led to a lack of clarity, we have expanded the description of the data analysis and added extensive explanations and supporting references for the mixed expert approach that was used throughout the analysis. We hope this is now clear.

Integrating a significant portion of the discussion section into the results section could enhance clarity. An explanation of the utility of machine learning in classifying patient groups over conventional methods and the citation of original research articles, rather than relying on review articles, may also add clarity to the usefulness of the study. 

As suggested by the reviewer, we moved the relevant parts from the discussion to the results section in the revised version of our manuscript.

Reviewer #1 (Recommendations For The Authors): 

Figure 2 should be better explained or removed. In its current form, it does not add to the interpretation of the manuscript.  

As mentioned above, we have expanded the description of the ESOM/U-matrix method in the Methods section and rewritten the figure legend. In addition, we have annotated the U-matrix in the figure. The method has been reported extensively in the computer science and biomedical literature, and a more detailed description in the referenced papers would go beyond the current focus on lipidomics. However, we believe that this discussion is sufficiently detailed for the readers of this report: "… a second unsupervised approach was used to verify the agreement between the lipidomics data structure and the prior classification, implemented as self-organizing maps (SOM) of artificial neurons (19). In the special form of an “emergent” SOM (ESOM (20)), the present map consisted of 4,000 neurons arranged on a two-dimensional toroidal grid with 50 rows and 80 columns (21, 22). ESOM was used because it has been repeatedly shown to correctly detect subgroup structures in biomedical data sets comparable to the present one (20, 22, 23). The core principle of SOM learning is to adjust the weights of neurons based on their proximity to input data points. In this process, the best matching unit (BMU) is identified as the neuron closest to a given data point. The adaptation of the weights is determined by a learning rate (η) and a neighborhood function (h), both of which gradually decrease during the learning process. Finally, the groups are projected onto separate regions of the map. On top of the trained ESOM, the distance structure in the high-dimensional feature space was visualized in the form of a so-called U-matrix (24) which is the canonical tool for displaying the distance structures of input data on ESOM (21). 

The visual presentation facilitates data group separation by displaying the distances between BMUs in high-dimensional space in a color-coding that uses a geographical map analogy, where large "heights" represent large distances in feature space, while low "valleys" represent data subsets that are similar. "Mountain ranges" with "snow-covered" heights visually separate the clusters in the data. Further details about ESOM can be found in (24)."

The second patient cohort is only included in the discussion - with cohort details in the supplementary material and figures included in the main text. Perhaps these data should be removed entirely. The findings are described as trends and not statistically significant and multiple issues with this second cohort are mentioned in the discussion. 

We agree with the reviewer that including the second patient cohort in the discussion is inadequate. Of course, there are differences between the patient cohorts that do not allow direct comparison and that are highlighted in the section on limitations of the study. However, we still think it is interesting and relevant to show these data, because we used our algorithms trained on the first patient cohort to analyze the second cohort. And these data support the main results. 

We therefore moved the entire paragraph to the results section of to improve coherence of our manuscript. The passage was introduced with the subheading:  “Support of the main results in an independent second patient cohort”.

The title does not reflect the content of the paper and should be changed to better reflect the content and its significance. 

We change the title to “Machine learning and biological validation identify sphingolipids as potential mediators of paclitaxel-induced neuropathy in cancer patients” to avoid overstating the results as suggested by the Reviewer.

Further, the discussion should be modified to avoid overstating the results. 

As the reviewer suggests, we changed the wording to avoid overstating the results. 

Reviewer #2 (Recommendations For The Authors): 

Please address the absence of clear neuropathy in the majority of patients after treatment with paclitaxel in your discussion. 

As stated above, occurrence and grade of the neuropathy are in line with the results from previous studies. From these studies, the expected occurrence of neuropathy with our therapeutic regimen is around 50-70%, (the variability is due to differences in the assessment methods) and most patients (80-90%) are expected to experience Grade 1 neuropathy after 12 weeks (1-3). 

We added this information in the discussion section of the revised manuscript.

Line 65: Kindly replace review articles with original research articles for proper citation. 

We replaced the review articles with original publications, focusing on clinical observations. We added the following publications: Jensen et al., Front Neurosci 2020; Chen et al., Neurobiol Aging 2018; Igarashi et al., J Alzheimers Dis. 2011; Kim et al., Oncotarget 2017 as references 17-20 in the revised version of our manuscript.

Line 260: The mention of SA1P is introduced here without prior reference (do not use words like "again", or "see above", if it is not previously mentioned). Adjust the text for coherence.

We agree with the reviewer that the introduction of SA1P in this passage in incoherent. We replaced the sentence in line 260 with: 

The small set of lipid mediators emerging from all three methods as informative for neuropathy included the sphingolipid sphinganine-1-phosphate (SA1P), also known as dihydrosphingosine-1-phosphate (DH-S1P)…”

Lines 301-315: Consider relocating several lines from this section to the results section for improved clarity. 

We moved the lines 309-312 explaining the algorithm selection and their validation success in the corresponding results section (Lipid mediators informative for assigning postpaclitaxel therapy samples to neuropathy).

Lines 382-396: Move this content to the results section to enhance the organization and coherence of the manuscript. 

We moved the entire paragraph to the results section of our manuscript to improve coherence. The passage was introduced with the subheading:  “Support of the main results in an independent second patient cohort”.

References

(1) Barginear M, Dueck AC, Allred JB, Bunnell C, Cohen HJ, Freedman RA, et al. Age and the Risk of Paclitaxel-Induced Neuropathy in Women with Early-Stage Breast Cancer (Alliance A151411): Results from 1,881 Patients from Cancer and Leukemia Group B (CALGB) 40101. Oncologist. 2019;24(5):617-23.

(2) Mauri D, Kamposioras K, Tsali L, Bristianou M, Valachis A, Karathanasi I, et al. Overall survival benefit for weekly vs. three-weekly taxanes regimens in advanced breast cancer: A metaanalysis. Cancer Treat Rev. 2010;36(1):69-74.

(3) Budd GT, Barlow WE, Moore HC, Hobday TJ, Stewart JA, Isaacs C, et al. SWOG S0221: a phase III trial comparing chemotherapy schedules in high-risk early-stage breast cancer. J Clin Oncol. 2015;33(1):58-64.

(4) Lötsch J, and Ultsch A. Pitfalls of Using Multinomial Regression Analysis to Identify ClassStructure-Relevant Variables in Biomedical Data Sets: Why a Mixture of Experts (MOE) Approach Is Better. BioMedInformatics. 2023;3(4):869-84.

(5) Kruskal WH, and Wallis WA. Use of Ranks in One-Criterion Variance Analysis. J Am Stat Assoc. 1952;47(260):583-621.

(6) Kramer R, Bielawski J, Kistner-Griffin E, Othman A, Alecu I, Ernst D, et al. Neurotoxic 1deoxysphingolipids and paclitaxel-induced peripheral neuropathy. FASEB J. 2015;29(11):4461-72.

(7) Field JJ, Diaz JF, and Miller JH. The binding sites of microtubule-stabilizing agents. Chem Biol. 2013;20(3):301-15.

(8) Janes K, Little JW, Li C, Bryant L, Chen C, Chen Z, et al. The development and maintenance of paclitaxel-induced neuropathic pain require activation of the sphingosine 1-phosphate receptor subtype 1. J Biol Chem. 2014;289(30):21082-97.

(9) Chua KC, Xiong C, Ho C, Mushiroda T, Jiang C, Mulkey F, et al. Genomewide Meta-Analysis Validates a Role for S1PR1 in Microtubule Targeting Agent-Induced Sensory Peripheral Neuropathy. Clin Pharmacol Ther. 2020;108(3):625-34.

(10) Kawakami K, Chiba T, Katagiri N, Saduka M, Abe K, Utsunomiya I, et al. Paclitaxel increases high voltage-dependent calcium channel current in dorsal root ganglion neurons of the rat. J Pharmacol Sci. 2012;120(3):187-95.

(11) Pittman SK, Gracias NG, Vasko MR, and Fehrenbacher JC. Paclitaxel alters the evoked release of calcitonin gene-related peptide from rat sensory neurons in culture. Exp Neurol. 2013.

(12) Luo H, Liu HZ, Zhang WW, Matsuda M, Lv N, Chen G, et al. Interleukin-17 Regulates NeuronGlial Communications, Synaptic Transmission, and Neuropathic Pain after Chemotherapy.

Cell reports. 2019;29(8):2384-97 e5.

(13) Pease-Raissi SE, Pazyra-Murphy MF, Li Y, Wachter F, Fukuda Y, Fenstermacher SJ, et al. Paclitaxel Reduces Axonal Bclw to Initiate IP3R1-Dependent Axon Degeneration. Neuron. 2017;96(2):373-86 e6.

(14) Duggett NA, Griffiths LA, and Flatters SJL. Paclitaxel-induced painful neuropathy is associated with changes in mitochondrial bioenergetics, glycolysis, and an energy deficit in dorsal root ganglia neurons. Pain. 2017.

(15) Li Y, Adamek P, Zhang H, Tatsui CE, Rhines LD, Mrozkova P, et al. The Cancer Chemotherapeutic Paclitaxel Increases Human and Rodent Sensory Neuron Responses to TRPV1 by Activation of TLR4. J Neurosci. 2015;35(39):13487-500.

(16) Hara T, Chiba T, Abe K, Makabe A, Ikeno S, Kawakami K, et al. Effect of paclitaxel on transient receptor potential vanilloid 1 in rat dorsal root ganglion. Pain. 2013;154(6):882-9.

(17) Jardin I, Lopez JJ, Diez R, Sanchez-Collado J, Cantonero C, Albarran L, et al. TRPs in Pain Sensation. Front Physiol. 2017;8:392.

(18) Julius D. TRP Channels and Pain. Annual review of cell and developmental biology.

2013;29:355-84.

(19) Kohonen T. Self-Organized Formation of Topologically Correct Feature Maps. Biol Cybern. 1982;43(1):59-69.

(20) Lötsch J, Lerch F, Djaldetti R, Tegder I, and Ultsch A. Identification of disease-distinct complex biomarker patterns by means of unsupervised machine-learning using an interactive R toolbox (Umatrix). Big Data Analytics. 2018;3(1):5.

(21) Ultsch A. 2003.

(22) Lotsch J, Geisslinger G, Heinemann S, Lerch F, Oertel BG, and Ultsch A. Quantitative sensory testing response patterns to capsaicin- and ultraviolet-B-induced local skin hypersensitization in healthy subjects: a machine-learned analysis. Pain. 2018;159(1):11-24.

(23) Lötsch J, Thrun M, Lerch F, Brunkhorst R, Schiffmann S, Thomas D, et al. Machine-Learned Data Structures of Lipid Marker Serum Concentrations in Multiple Sclerosis Patients Differ from Those in Healthy Subjects. Int J Mol Sci. 2017;18(6).

(24) Lötsch J, and Ultsch A. Cham: Springer International Publishing; 2014:249-57.

Author response:

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

Public Reviews:

Reviewer 1 (Public Review):

Summary:

The authors propose that the energy landscape of animals can be thought of in the same way as the fundamental versus realized niche concept in ecology. Namely, animals will use a subset of the fundamental energy landscape due to a variety of factors. The authors then show that the realized energy landscape of eagles increases with age as the animals are better able to use the energy landscape. Strengths:

This is a very interesting idea and that adds significantly to the energy landscape framework. They provide convincing evidence that the available regions used by birds increase with size.

Weaknesses:

Some of the measures used in the manuscript are difficult to follow and there is no mention of the morphometrics of birds or how these change with age (other than that they don’t change which seems odd as surely they grow). Also, there may need to be more discussion of other ontogenetic changes such as foraging strategies, home range size etc.

We thank reviewer 1 for their interest in our study and for their constructive recommendations. We have included further discussions of these points in the manuscript and outline these changes in our responses to the detailed recommendations below.

Reviewer 2 (Public Review):

Summary:

With this work, the authors tried to expand and integrate the concept of realized niche in the context of movement ecology by using fine-scale GPS data of 55 juvenile Golden eagles in the Alps. Authors found that ontogenic changes influence the percentage of area flyable to the eagles as individuals exploit better geographic uplifts that allow them to reduce the cost of transport.

Strengths:

Authors made insightful work linking changes in ontogeny and energy landscapes in large soaring birds. It may not only advance the understanding of how changes in the life cycle affect the exploitability of aerial space but also offer valuable tools for the management and conservation of large soaring species in the changing world.

Weaknesses:

Future research may test the applicability of the present work by including more individuals and/or other species from other study areas.

We are thankful to reviewer 2 for their encouragement and positive assessment of our work. We have addressed their specific recommendations below.

Recommendations for the authors:

Reviewer 1 (Recommendations For The Authors):

I found this to be a very interesting paper which adds some great concepts and ideas to the energy landscape framework. The paper is also concise and well-written. While I am enthusiastic about the paper there are areas that need clarifying or need to be made clearer. Specific comments below:

Line 64: I disagree that competition is the fundamental driver of the realized niche. In some cases, it may be but in others, predation may be far more important (as an example).

We agree with this point and have now clarified that competition is an example of a driver of the realized niche. We have also included predation as another example:

"However, just as animals do not occupy the entirety of their fundamental Hutchinsonian niche in reality [1], for example due to competition or predation risk, various factors can contribute to an animal not having access to the entirety of its fundamental movement niche."

Intro: I think the authors should emphasize that morphological changes with ontogeny will change the energy landscape for many animals. It may not be the case specifically with eagles but that won’t be true for other animals. For example, in many sharks, buoyancy increases with age.

We agree and have now clarified that the developmental processes that we are interested in happen in addition to morphological changes:

"In addition to morphological changes, as young animals progress through their developmental stages, their movement proficiency [2] and cognitive capabilities [3] improve and memory manifests [4]."

Line 91-93: The idea that birds fine-tune motor performance to take advantage of updrafts is a very important one to the manuscript and should be discussed in a bit more detail. How? At the moment there is a single sentence and it doesn’t even have a citation yet this is the main crux of the changes in realized energy landscape with age. This point should be emphasized because, by the end of the introduction, it is not clear to me why the landscape should be cheaper as the birds age?

Thank you for pointing out this missing information. We have now added examples to clarify how soaring birds fine-tune their motor performance when soaring. These include for example adopting high bank angles in narrow and weak thermals [5] and reducing gliding airspeed when the next thermal has not been detected [6]:

"Soaring flight is a learned and acquired behavior [7, 8], requiring advanced cognitive skills to locate uplifts as well as fine-tuned locomotor skills for optimal adjustment of the body and wings to extract the most energy from them, for example by adopting high bank angles in narrow and weak thermals [5] and reducing gliding airspeed when the next thermal has not been detected [6]."

Results:

Line 106: explain the basics of the life history of the birds in the introduction. I have no idea what emigration refers to or the life history of these animals.

Thank you for pointing out the missing background information. We have now added this

information to the introduction:

"We analyzed 46,000 hours of flight data collected from bio-logging devices attached to 55 wild-ranging golden eagles in the Central European Alps. These data covered the transience phase of natal dispersal (hereafter post-emigration). In this population, juveniles typically achieve independence by emigrating from the parental territory within 4-10 months after fledging. However, due to the high density of eagles and consequently the scarcity of available territories, the transience phase between emigration and settling by eventually winning over a territory is exceptionally long at well over 4 years. Our hypothesis posited that the realized energy landscape during this transience phase gradually expands as the birds age."

What I still am having a hard time understanding is the flyability index. Is this just a measure of the area animals actively select and then the assumption that it’s a good region to fly within?

We have modified our description of the flyability index for more clarity. In short, we built a step-selection model and made predictions using this model. The predictions estimate the probability of use of an area based on the predictors of the model. For the purpose of our study and what our predictors were (proxies for uplift + movement capacity), we interpreted the predicted values as the "flyability index". We have now clarified this in the methods section:

"We made the predictions on the scale of the link function and converted them to values between 0 and 1 using the inverse logit function [9]. These predicted values estimated the probability of use of an area for flying based on the model. We interpreted these predicted values as the flyability index, representing the potential energy available in the landscape to support flight, based on the uplift proxies (TRI and distance to ridge line) and the movement capacity (step length) of the birds included in the model."

It might also be useful to simply show the changes in the area the animals use with age as well (i.e. a simple utilization distribution). This should increase in age for many animals but would also be a reflection of the resources animals need to acquire as they get older.

We have now added the figure S2 to the supplementary material. This plot was created by calculating the cumulative area used by the birds in each week after emigration. This was done by extracting the commuting flights for each week, converting these to line objects, overlapping the lines with a raster of 100*100 m cell size, counting the number of overlapping cells and calculating the area that they covered. We did not calculate UDs or MCPs because the eagles seem to be responding to linear features of the landscape, e.g. preferring ridgelines and avoiding valleys. Using polygons to estimate used areas would have made it difficult to ensure that decision-making with regards to these linear features was captured.

In a follow-up project, a PhD student in the golden eagle consortium is exploring the individuals’ space use after emigration considering different environmental and social factors. The outcome of that study will further complete our understanding of the post-emigration behavior of juvenile golden eagles in the Alps.

How much do the birds change in size over the ontogeny measured? This is never discussed.

Thank you for bringing up this question. The morphometrics of juvenile golden eagles are not significantly different from the adults, except in the size of culmen and claws [10]. Body mass changes after fledging, because of the development of the pectoral muscles as the birds start flying. Golden eagles typically achieve adult-like size and mass within their natal territory before emigration, at which time we started quantifying the changes in energy landscape. Given our focus on post-emigration flight behavior, we do not expect any significant changes in size and body mass during our study period. We now cover this in the discussion:

"Juvenile golden eagles complete their morphological development before gaining independence from their parents, with their size and wing morphology remaining stable during the post-emigration phase [10, 11]. Consequently, variations in flyability of the landscape for these birds predominantly reflect their improved mastery of soaring flight, rather than changes in their morphology."

Discussion:

Line 154: Could the increase in step length also be due to changes in search strategies with age? e.g. from more Brownian motion when scavenging to Levy search patterns when actively hunting?

This is a very good point and we tried to look for evidence of this transition in the tracking data. We explored the first passage time for two individuals with a radius of 50 km to see if there is a clear transition from a Brownian to a Levy motion. The patterns that emerge are inconclusive and seem to point to seasonality rather than a clear transition in foraging strategy (Author response image 1). We have modified our statement in the discussion about the change in preference of step lengths indicating improve flight ability, to clarify that it is speculative:

Author response image 1.

First passage times using a 50 km radius for two randomly selected individuals.

"Our findings also reveal that as the eagles aged, they adopted longer step lengths, which could indicate an increasing ability to sustain longer uninterrupted flight bouts."

Methods:

Line 229: What is the cutoff for high altitude or high speed?

We used the Expectation-maximization binary clustering (EMbC) method to identify commuting flights. The EmbC method does not use hard cutoffs to cluster the data. Each data point was assigned to the distribution to which it most likely belonged based on the final probabilities after multiple iterations of the algorithm. Author response image 2 shows the distribution of points that were either used or not used based on the EmbC classification.

Author response image 2.

Golden eagle tracking points were either retained (used) or discarded (not used) for further data analysis based on the EmbC algorithm. The point were clustered based on ground speed and height above ground.

Figure 1: The figure captions should stand on their own but in this case there is no information as to what the tests are actually showing.

We have now updated the caption to provide information about the model:

"Coefficient estimates of the step selection function predicting probability of use as a function of uplift proxies, week since emigration, and step length. All variables were z-transformed prior to modeling.

The error bars show 95% confidence intervals."

Reviewer 2 (Recommendations For The Authors):

First, I want to congratulate you on this fantastic work. I enjoyed reading it. The manuscript is clear and well-written, and the findings are sound and relevant to the field of movement ecology. Also, the figures are neatly presented and easy to follow.

I particularly liked expanding the old concept of fundamental vs realized niche into a movement ecology context. I believe that adds a fresh view into these widely accepted ecological assumptions on species niche, which may help other researchers build upon them to better understand movement "realms" on highly mobile animals in a rapidly changing world.

I made some minor comments to the manuscript since it was hard to find important weaknesses in it, given the quality of your work. However, there was a point in the discussion that I feel deserves your attention (or rather a reflection) on how major biological events such as moulting could also influence birds to master the flying and exploitation of the energy landscape. You may find my suggestion quite subjective, but I think it may help expand your idea for future works and, what is more, link concepts such as energy landscapes, ontogeny, and important life cycle events such as moulting in large soaring birds. I consider this relevant from a mechanistic perspective to understand better how individuals negotiate all three concepts to thrive and persist in changing environments and to maximise their

fitness.

Once again, congratulations on this excellent piece of research.

We thank the reviewer for their enthusiasm about our work and for bringing up important points about the biology of the species. Our detailed response are below.

MINOR COMMENTS:

(Note: Line numbers refer to those in the PDF version provided by the journal).

Line 110: Distinguished (?)

corrected

Line 131: Overall, I agree with the authors’ discussion and very much liked how they addressed crucial points. However, I have a point about some missing non-discussed aspects of bird ecology that had not been mentioned.

The authors argue that morphological traits are less important in explaining birds’ mastery of flight (thus exploiting all available options in the landscape). However, I think the authors are missing some fundamental aspects of bird biology that are known to affect birds’ flying skills, such as moult.

The moulting process affects species’ flying capacity. Although previous works have not assessed moults’ impact on movement capacity, I think it is worth including the influence of flyability on this ecologically relevant process.

For instance, golden eagles change their juvenile plumage to intermediate, sub-adult plumage in two or three moult cycles. During this process, the moulting process is incomplete and affects the birds’ aerodynamics, flying capacity, and performance (see Tomotani et al. 2018; Hedenström 2023). Thus, one could expect this process to be somewhat indirectly linked to the extent to which birds can exploit available resources.

Hedenström, A. (2023). Effects of wing damage and moult gaps on vertebrate flight performance.

Journal of Experimental Biology, 226(9), jeb227355. Tomotani, B. M., Muijres, F. T., Koelman, J., Casagrande, S., & Visser, M. E. (2018). Simulated moult reduces flight performance, but overlap with breeding does not affect breeding success in a longdistance migrant. Functional Ecology, 32(2), 389-401.

We thank the reviewer for bringing up this relevant topic. We explored the literature listed by the reviewer and also other sources. We came to the conclusion that moulting does not impact our findings. In our study, we included data for eagles that had emigrated from the natal territories, with their fully grown feathers in juvenile plumage. The moulting schedule in juvenile birds is similar to that of adults: the timing, intensity, and sequence of feathers being replaced is consistent every year (Author response image 3). For these reasons, we do not believe that moulting stage noticeably impacts flight performance at the scale of our study (hourly flights). Fine details of soaring flight performance (aerodynamics within and between thermals) could differs during moulting of different primary and secondary feathers, but this is something that would occur every time the eagle replaces these feather and we do not expect it to be any different for juveniles. Such fine scale investigations are outside the scope of this study.

Author response image 3.

Moulting schedule of golden eagles [12]

Lines 181-182: I don’t think trophic transitions rely only on individual flying skill changes. Furthermore, despite its predominant role, scavenging does not mean it is the primary source of food acquisition in golden eagles. This also depends on prey availability, and scavenging is an auxiliary font of easy-to-catch food.

Scavenging implies detecting carcasses. Should this carcass appearance occur in highly rugged areas, the likelihood of detection also reduces notably. This is not to say that there are not more specialized carrion consumers, such as vultures, that may outcompete eagles in searching for such resources more

efficiently.

In summary, I don‘t think such transition relies only on flying skills but on other non-discussed factors such as knowledge accumulation of the area or even the presence of conspecifics.

Line 183: This is precisely what I meant with my earlier comment.

Thank you for the discussion on the interaction between flight development and foraging strategy. We explored the transition from scavenging to hunting above as a response to Reviewer 1, but did not find a clear transition. This is in line with your comment that the birds probably use both scavenging and hunting methods opportunistically.

Lines 193-195: I will locate this sentence somewhere in this paragraph. As it is now, it seems a bit out of context. It could be a better fit at the end of the first point in line 203.

Thank you for pointing out the issue with the flow. We have now added a transitional sentence before this one to improve the paragraph. The beginning of the conclusion now reads as follows, with the new sentence shown in boldface.

"Spatial maps serve as valuable tools in informing conservation and management strategies by showing the general distribution and movement patterns of animals. These tools are crucial for understanding how animals interact with their environment, including human-made structures. Within this context, energy landscapes play an important role in identifying potential areas of conflict between animals and anthropogenic infrastructures such as wind farms. The predictability of environmental factors that shape the energy landscape has facilitated the development of these conservation tools, which have been extrapolated to animals belonging to the same ecological guild traversing similar environments."

References

(1) Colwell, R. K. & Rangel, T. F. Hutchinson’s duality: The once and future niche. Proceedings of the National Academy of Sciences 106, 19651–19658. doi:10.1073/pnas.0901650106 (2009).

(2) Corbeau, A., Prudor, A., Kato, A. & Weimerskirch, H. Development of flight and foraging behaviour in a juvenile seabird with extreme soaring capacities. Journal of Animal Ecology 89, 20–28. doi:10.1111/1365-2656.13121 (2020).

(3) Fuster, J. M. Frontal lobe and cognitive development. Journal of neurocytology 31, 373–385.

doi:10.1023/A:1024190429920 (2002).

(4) Ramsaran, A. I., Schlichting, M. L. & Frankland, P. W. The ontogeny of memory persistence and specificity. Developmental Cognitive Neuroscience 36, 100591. doi:10.1016/j.dcn.2018.09.002 (2019).

(5) Williams, H. J., Duriez, O., Holton, M. D., Dell’Omo, G., Wilson, R. P. & Shepard, E. L. C. Vultures respond to challenges of near-ground thermal soaring by varying bank angle. Journal of Experimental Biology 221, jeb174995. doi:10.1242/jeb.174995 (Dec. 2018).

(6) Williams, H. J., King, A. J., Duriez, O., Börger, L. & Shepard, E. L. C. Social eavesdropping allows for a more risky gliding strategy by thermal-soaring birds. Journal of The Royal Society Interface 15, 20180578. doi:10.1098/rsif.2018.0578 (2018).

(7) Harel, R., Horvitz, N. & Nathan, R. Adult vultures outperform juveniles in challenging thermal soaring conditions. Scientific reports 6, 27865. doi:10.1038/srep27865 (2016).

(8) Ruaux, G., Lumineau, S. & de Margerie, E. The development of flight behaviours in birds. Proceedings of the Royal Society B: Biological Sciences 287, 20200668. doi:10.1098/rspb.2020.

0668 (2020).

(9) Bolker, B., Warnes, G. R. & Lumley, T. Package gtools. R Package "gtools" version 3.9.4 (2022).

(10) Bortolotti, G. R. Age and sex size variation in Golden Eagles. Journal of Field Ornithology 55,

54–66 (1984).

(11) Katzner, T. E., Kochert, M. N., Steenhof, K., McIntyre, C. L., Craig, E. H. & Miller, T. A. Birds of the World (eds Rodewald, P. G. & Keeney, B. K.) chap. Golden Eagle (Aquila chrysaetos), version 2.0. doi:10.2173/bow.goleag.02 (Cornell Lab of Ornithology, Ithaca, NY, USA, 2020).

(12) Bloom, P. H. & Clark, W. S. Molt and sequence of plumages of Golden Eagles and a technique for in-hand ageing. North American Bird Bander 26, 2 (2001).

Author response:

(1) Clarification and Detailed Explanation in the Methods Section:

- Regarding Reviewer 1's comments about the unclear explanation of the update process for pseudotime, T, and the selection of important genes/features at bifurcation points in the methods, we will provide a detailed description of the update process for pseudotime T and how high-weight genes important to the bifurcation process are selected.

- Regarding Reviewer 2's comments concerning the impact of the initial pseudotime prediction method and the insufficient description of various parameters, we will add information about the differences in the initially used pseudotime prediction methods and provide detailed information on the techniques and parameters used in each analysis.

- Regarding Reviewer 2's comments on the choice of kernel functions, we will explain the rationale for selecting rbf and polynomial kernels and why other options were discarded.

(2) Performance Comparison and Data Presentation:

- Regarding Reviewer 1's comments about using a few trajectory plots of the real-world data to visualize the results, we will include 1-2 trajectory plots of real-world datasets in the benchmark analysis to better visualize the results and assess accuracy.

- Regarding Reviewer 2's comments concerning the lack of comparison results and discussion related to trajectory prediction methods based on deep learning, we will include a comparison with deep learning methods such as scTour and Tigon in the revision. Additionally, we will discuss the latest deep learning methods for bifurcation analysis and alternative trajectory inference methods such as CellRank.

- Regarding Reviewer 2's comments on the impact of MURP, we will include an analysis on whether the number of MURPs affects the performance of the method and compare it with the random subsampling approach.

(3) Article Calibration and Refinement:

- Regarding Reviewer 2's comments on the discussion section, we will simplify the first three paragraphs to succinctly convey the background and implications of our contributions. Additionally, we will explain why HVG is considered as the entire feature space in our comparisons and analyses.

- Regarding Reviewer 2's comments concernig the regulons in the microglia analysis, we will review the correct explanations and revise the article accordingly.

- In response to the issues raised by both reviewers regarding grammatical errors, spelling mistakes, and inconsistencies between text and figures, we will review and correct any errors in the article. This includes providing explanations for all abbreviations upon their first appearance, ensuring the accuracy of text and figure descriptions, correcting equation numbering, improving image quality, and revising descriptions such as "the current manifold learning methods face two major challenges."

(4) Enhancing Descriptions and Readability:

- Regarding Reviewer 1's comments about the synthetic data, we will add a brief description in the main text on how synthetic data were generated.

- Regarding Reviewer 1's comments on the survival analysis, we will provide a more detailed description of the computational steps and clarify whether key confounding factors such as age, clinical stage, and tumor purity were controlled.

- Regarding Reviewer 2's comments on evaluation metrics, we will add detailed descriptions of the evaluation metrics and provide intuitive explanations of how different methods perform across various metrics in the comparison results.

- Regarding Reviewer 2's comments on CD8+ T cells, we plan to compare MGPfact with Monocle3, in addition to Monocle2. This will help clarify the added value of MGPfact and provide a more comprehensive evaluation of its performance.

- Regarding Reviewer 2's comments about consensus trajectorie, we will add detailed descriptions of the process of generating consensus trajectories.

- Regarding Reviewer 2's comments on regulons, we will include additional information on the process of downstream trajectory analysis and clarify the roles of SCENIC, GENIE3, RCisTarget, and AUCell in the bifurcation analysis.

Author response:

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

Preliminary note from the Reviewing Editor:

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

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

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

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

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

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

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

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

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

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

Weaknesses:

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

Reviewer #2 (Public Review):

Summary:

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

Strengths:

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

Weaknesses:

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

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

Major:

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

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

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

Author response image 1.

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

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

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

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

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

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

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

Minor:

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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Author response:

The authors intend to submit a revised manuscript that addresses the questions raised in the public reviews.

Author response:

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

eLife assessment

This valuable contribution studies factors that impact molecular exchange between dense and dilute phases of biomolecular condensates through continuum models and coarse-grained simulations. The authors provide solid evidence that interfacial resistance can cause molecules to bounce off the interface and limit mixing. Results like these can inform how experimental results in the field of biological condensates are interpreted.

We would like to sincerely thank the editors for spending time on our manuscript and for the very positive assessment of our work. We have carefully considered and addressed the reviewers’ comments in the point-by-point response below and have revised our manuscript accordingly.

Reviewer #1 (Public Review):

Summary:

In this paper by Zhang, the authors build a physical framework to probe the mechanisms that underlie the exchange of molecules between coexisting dense and dilute liquid-like phases of condensates. They first propose a continuum model, in the context of a FRAP-like experiment where the fluorescently labeled molecules inside the condensate are bleached at t=0 and the recovery of fluorescence is measured. Through this model, they identify how the key timescales of internal molecular mixing, replenishment from dilute phase, and interface transfer contribute to molecular exchange timescale. Motivated by a recent experiment reported by some of the co-authors previously (Brangwynne et al. in 2019) finding strong interfacial resistance in in-vitro protein droplets of LAF-1, they seek to understand the microscopic features contributing to the interfacial conductance (inversely proportional to the resistance). To check, they perform coarse-grained MD simulations of sticker-spacer self-associative polymers and report how conductance varies significantly even across the few explored sequences. Further, by looking at individual trajectories, they postulate that "bouncing" - i.e., molecules that approach the interface but are not successfully absorbed - is a strong contributor to this mass transfer limitation. Consistent with their predictions, sequences that have more free unbound stickers (i.e., for example through imbalance sequence sticker stoichiometries) have higher conductances and they show a simple linear scaling between the number of unbound stickers and conductance. Finally, they predict a droplet-size-dependent transition in recovery time behavior.

Strengths:

(1) This paper is well-written overall and clear to understand.

(2) By combining coarse-grained simulations, continuum modeling, and comparison to published data, the authors provide a solid picture of how their proposed framework relates to molecular exchange mechanisms that are dominated by interface resistance and LAF-1 droplets.

(3) The choice of different ways to estimate conductance from simulation and reported data are thoughtful and convincing in their near agreement (although a little discussion of why and when they differ would be merited as well).

We would like to thank the reviewer for the positive evaluation of our work. Indeed, we are grateful to the reviewer for this thoughtful, detailed, and constructive report, which has helped us strengthen the manuscript.

Weaknesses:

(1) Almost the entirety of this paper is motivated by a previously reported FRAP experiment on a particular LAF-1 droplet in vitro. There are a few major concerns I have with how the original data is used, how these results may generalize, and the lack of connection of predictions with any other experiments (published or new).

a. The mean values of cdense, cdilute, diffusivities, etc. are taken from Taylor et al. to rule in the importance of interfacial mass transfer limits. While this may be true, the values originally inferred (in the 2019 paper that this paper is strongly built off) report extremely large confidence intervals/inferred standard errors. The authors should accordingly report all their inferences with correct standardized errors or confidence intervals, which in turn, allow us to better understand these data.

Yes, agreed. We have now included the standard errors of the parameters from Taylor et al. (2019), and reported the corresponding standard errors for the timescales and interface conductance using error propagation. We have modified Fig. 1C right panel as well as the text in the figure caption:

“(Right) Expected recovery times and if the slowest recovery process was either the flux from the dilute phase or diffusion within the droplet, respectively, with and taken from Taylor et al. (2019). While the timescale associated with interface resistance is unknown, the measured recovery time is much longer than and , suggesting the recovery is limited by flux through the interface, with an interface conductance of  (Below Figure 1)”

b. The generalizability of this model is hard to gauge when all comparisons are made to a single experiment reported in a previous paper.

i. Conceptually, the model is limited to single-component sticker-spacer polymers undergoing phase separation which is already a very simplified model of condensates - for e.g., LAF1 droplets in the cell have no perceptible interfacial mass limitations, also reported in Taylor et al. 2019 - so how these mechanisms relate to living systems as opposed to specific biochemistry experiments. So the authors need to discuss the implications and limitations of their model in the living context where there are multiple species, finite-size effects, and active processes at play.

We thank the reviewer for the critical comment. To address this point, we have included a paragraph in the Discussion regarding in vivo situations:

“In this work, we focused on the exchange dynamics of in vitro single-component condensates. How is the picture modified for condensates inside cells? It has been shown that Ddx4-YFP droplets in the cell nucleus exhibit negligible interface resistance Taylor et al. (2019), which raises the question whether interface resistance is relevant to natural condensates in vivo. Future quantitative FRAP and single-molecule tracking experiments on different types of droplets in the cell will address this question. One complication is that condensates in cells are almost always multi-component, which can increase the complexity of the exchange dynamics. Interestingly, formation of multiple layers or the presence of excess molecules of one species coating the droplet is likely to increase interface resistance. A notable example is the Pickering effect, in which adsorbed particles partially cover the interface, thereby reducing the accessible area and the overall condensate surface tension, slowing down the exchange dynamics Folkmann et al. (2021). The development of theory and modeling for the exchange dynamics of multi-component condensates is currently underway. (Lines 323-334)”

ii. Second, can the authors connect their model to make predictions of the impact of perturbations to LAF-1 on exchange timescales? For example, are mutants (which change the number or positioning of "stickers") expected to show particular trends in conductances or FRAP timescales? Since LAF-1 is a relatively well-studied protein in vitro, can the authors further contrast their expectations with already published datasets that explore these perturbations, even if they don't generate new data?

Our model is intended to address interface exchange dynamics at the conceptual level. The underlying mechanism for the large interface resistance of LAF-1 droplets could be more complicated than explored in our work. To study the impact of perturbations to LAF-1 on exchange timescales likely requires substantially more sophisticated molecular dynamics simulations. We undertook an extensive search for FRAP experiments on LAF-1 droplets where the whole droplet is photobleached, but were not able to find another dataset. We would be grateful if the reviewer is aware of such data and can point us to it.

iii. A key prediction of the interface limitation model is the size-dependent crossover in FRAP dynamics. Can the authors reanalyze published data on LAF-1 (albeit of different-size droplets) to check their predictions? At the least, is the crossover radius within experimentally testable limits?

Based on our prediction, the crossover radius for LAF-1 droplet is around 70 𝜇m. We have added a sentence in the text to point this out:

“We also predict the crossover for LAF-1 droplets to be around 𝑅 = 71 𝜇m, which in principle can be tested experimentally. (Lines 285-286)”

Unfortunately, most of FRAP experiments in Taylor at al. (2019) are partial FRAP experiments, in which only part of the dense phase is photobleached. The recovery time for such experiments reflects primarily the internal mixing speed of the dense phase rather than the exchange dynamics at the interface or transport from the dilute phase.

c. The authors nicely relate the exchange timescale to various model parameters. Is LAF-1 the only protein for which the various dilute/dense concentrations/diffusivities are known? Given the large number of FRAP and other related studies, can the authors report on a few other model condensate protein systems? This will help broaden the reach of this model in the context of other previously reported data. If such data are lacking, a discussion of this would be important.

Yes, indeed, we have found numerous publications with FRAP experiments performed on whole droplets of various proteins. However, none of these have provided a complete set of parameters to allow a quantitative analysis. Part of the reason is because it is nontrivial to have an accurate measurement of the partition coefficient (cden/cdil). We have added a sentence in the Discussion to promote future quantitative experiment and analysis of condensate exchange dynamics:

“We hope that our study will motivate further experimental investigations into the anomalous exchange dynamics of LAF-1 droplets and potentially other condensates, and the mechanisms underlying interface resistance. (Lines 320-322)”

To broaden the audience for this work in the hope of stimulating such studies, we have also modified the title and abstract so that it will be more visible to the FRAP community:

“The exchange dynamics of biomolecular condensates (Line 1)”

“A hallmark of biomolecular condensates formed via liquid-liquid phase separation is that they dynamically exchange material with their surroundings, and this process can be crucial to condensate function. Intuitively, the rate of exchange can be limited by the flux from the dilute phase or by the mixing speed in the dense phase. Surprisingly, a recent experiment suggests that exchange can also be limited by the dynamics at the droplet interface, implying the existence of an “interface resistance”. Here, we first derive an analytical expression for the timescale of condensate material exchange, which clearly conveys the physical factors controlling exchange dynamics. We then utilize sticker-spacer polymer models to show that interface resistance can arise when incident molecules transiently touch the interface without entering the dense phase, i.e., the molecules “bounce” from the interface. Our work provides insight into condensate exchange dynamics, with implications for both natural and synthetic systems. (Lines 16-26)”

(2) The reported sticker-spacer simulations, while interesting, represent a very small portion of the parameter space. Can the authors - through a combination of simulation, analyses, or physical reasoning, comment on how the features of their underlying microscopic model (sequence length, implicit linker length, relative stoichiometry of A/B for a given length, overall concentration, sequence pattern properties like correlation length) connect to conductance? This will provide more compelling evidence relating their studies beyond the cursory examination of handpicked sequences. A more verbose description of some of the methods would be appreciated as well, including specifically how to (a) calculate the bond lifetime of isolated A-B pair, and (b) how equilibration/convergence of MD simulations is established.

In our simulation, the interface conductance is essentially controlled by the fraction of unbound stickers, the encounter rate of a pair of unbound stickers, the dilute- and dense-phase concentrations, and the width of the interface. As a result, weaker binding strength and/or deviation of A:B stoichiometry from 1:1 result in a higher interface conductance. A6B6 polymers with long blocks of stickers of the same type (compared to (A2B2)3 and (A3B3)2) have a lower dilute-phase concentration and thinner interface width, so lower conductance. Sequence length and implicit linker length can have more complex effects, which are beyond the scope of the current study. We have now provided an explicit expression for 𝜅 in Equation (14) and added a discussion sentence in the text:

“More generally, we find that the interface conductance of the sticker-spacer polymers is controlled by the encounter rate of a pair of unbound stickers and the availability of these stickers, which in turn depends on the sticker-sticker binding strength, the dilute- and dense-phase polymer concentrations, and the width of the interface:

where 𝓃 is the number of monomers in a polymer,  is the global stoichiometry (i.e., ), and are the fractions of unbound A/B monomers in the dilute and dense phases. (Lines 208-214)”

We have also added a few sentences in Appendix 2 to describe how we calculate the bond lifetime of an isolated A-B pair and how equilibration in simulations is established.

“Briefly, the bond lifetime of an isolated pair is obtained by simulating a bound pair of A-B stickers in a box and recording the time when they first separate by the cutoff distance of the attractive interaction nm. The mean bond lifetime 𝜏 is found by averaging results of 1000 replicates with different random seeds. (Lines 642-645)”

“To test if the system has reached equilibrium, we compare the dense- and dilute-phase concentrations derived from the first and second halves of the recorded data. The agreement indicates that the system has reached equilibrium. (Lines 586-589)”

(3) A lot of the main text repeats previously published models (continuum ones in Taylor et al. 2019 and Hubsatch et al., 2021, amongst others) and the idea of interface resistance being limiting was already explored quantitatively in Taylor 2019 (including approximate estimates of mass transfer limitations) - this is fine in context. While the authors do a good job of referring to past work in context, the main results of this paper, in my reading, are:

- a simplified physical form relating conductance timescales.

- sticker-spacer simulations probing microscopic origins.

- analysis of size-dependent FRAP scaling.

I am stating this not as a major weakness, but, rather - I would recommend summarizing and categorizing the sections to make the distinctions between previously reported work and current advances sufficiently clear.

We thank the reviewer for a clear summary of the contributions of our work. We have highlighted our main contributions in multiple places:

“Here, we first derive an analytical expression for the timescale of condensate material exchange, which clearly conveys the physical factors controlling exchange dynamics. We then utilize sticker-spacer polymer models to show that interface resistance can arise when incident molecules transiently touch the interface without entering the dense phase, i.e., the molecules “bounce” from the interface. (Lines 21-25)”

“In the following, we first derive an analytical expression for the timescale of condensate material exchange, which conveys a clear physical picture of what controls this timescale. We then utilize a “sticker-spacer” polymer model to investigate the mechanism of interface resistance. We find that a large interface resistance can occur when molecules bounce off the interface rather than being directly absorbed. We finally discuss characteristic features of the FRAP recovery pattern of droplets when the exchange dynamics is limited by different factors. (Lines 65-70)”

“Specifically, we first derived an analytical expression for the exchange rate, which conveys the clear physical picture that this rate can be limited by the flux of molecules from the dilute phase, by the speed of mixing inside the dense phase, or by the dynamics of molecules at the droplet interface. Motivated by recent FRAP measurements Taylor et al. (2019) that the exchange rate of LAF-1 droplets can be limited by interface resistance, which contradicts predictions of conventional mean-field theory, we investigated possible physical mechanisms underlying interface resistance using a “sticker-spacer” model. Specifically, we demonstrated via simulations a notable example in which incident molecules have formed all possible internal bonds, and thus bounce from the interface, giving rise to a large interface resistance. Finally, we discussed the signatures in FRAP recovery patterns of the presence of a large interface resistance. (Lines 291-300)”

Reviewer #2 (Public Review):

Summary:

In this paper, the authors have obtained an analytical expression that provides intuition about regimes of interfacial resistance that depend on droplet size. Additionally, through simulations, the authors provide microscopic insight into the arrangement of sticky and non-sticky functional groups at the interface. The authors introduce bouncing dynamics for rationalizing quantity recovery timescales.

I found several sections that felt incomplete or needed revision and additional data to support the central claim and make the paper self-contained and coherent.

We thank the reviewer for spending time on our manuscript and for the helpful critical comments.

First, the analytical theory operates with diffusion coefficients for dilute and dense phases. For the dilute phase, this is fine. For the dense phase, I have doubts that dynamics can be described as diffusive. Most likely, dynamics is highly subdiffusive due to crowded, entangled, and viscoelastic environments of densely packed interactive biomolecules. Some explanation and justification are in order here.

The reviewer is correct in noting that molecules within a condensate can move subdiffusively due to the viscoelastic nature of the condensate. However, subdiffusion only occurs at short time and small length scales, the motion of molecules becomes diffusive at longer time and larger length scales. The crossover time here is the terminal relaxation time measured to be on the order of milliseconds to seconds for typical condensates (see Alshareedah, Ibraheem, et al. "Determinants of viscoelasticity and flow activation energy in biomolecular condensates" Science Advances 10.7, 2024). We previously have also found that, for sticker-spacer polymers, this relaxation time is determined by the time it takes for a sticker to switch to a new partner (see Ronceray et al. (2022) in References), which is therefore largely determined by the bond lifetime of a sticker pair. The crossover length scale is expected to be comparable to the size of a molecule based on the theory of polymer disentanglement. Importantly, in order for the bleached droplet to recover its fluorescence, the bleached molecules must travel for a much longer time and a much larger length than the crossover time and length. It is therefore expected that the molecules move diffusively on the relevant timescale of a FRAP experiment, albeit with a diffusion coefficient that reflects crowding and entanglement on short time and length scales.

The second major issue is that I did not find a clean comparison of simulations with the derived analytical expression. Simulations test various microscopic properties on the value of k, which is important. But how do we know that it is the same quantity that appears in the expressions? Also, how can we be sure that analytical expressions can guide simulations and experiments as claimed? The authors should provide sound evidence of the predictive aspect of their derived expressions.

We thank the reviewer for raising this critical issue. We agree with the reviewer that we did not perform an explicit simulation to validate the developed theory, which leaves a gap between our theory and simulations. The main reason is because simulation of an in silico “FRAP experiment” on a 3D droplet is very computationally costly. Nevertheless, following the reviewer’s suggestion, we have now performed such a simulation in which we “bleached” a small A6B6 droplet and measured its recovery time. The good agreement between simulation and theory helps validate our overall combined computational and analytical approach. We have incorporated the new simulation and results into the manuscript. Two new sections including new figures (Figure 4 and Appendix 2 Figure 4) are added: “Direct simulation of droplet FRAP” in the main text (lines 232-261) and “Details of simulation and theory of FRAP recovery of an A6B6 droplet” in Appendix 2 (lines 665-715).

Are the plots in Figure 4 coming from experiment, theory, and simulation? I could not find any information either in the text or in the caption.

Figure 4 (now Figure 5) is from theory which uses parameters of the A6B6 system in simulation. We have added the following sentences to clarify:

“We compare the measured FRAP recovery time for the small droplet (green circle) to theoretical predictions from Equation (6) (gray) and Equations (1) - (4) (black) in Figure 5A. (Lines 255-257)”

“Figure 5. FRAP recovery patterns for large versus small droplets can be notably different for condensates with a sufficiently large interface resistance. (A) Expected relaxation time as a function of droplet radius for in silico “FRAP experiments” on the A6B6 system. The interface resistance dominates recovery times for smaller droplets, whereas dense-phase diffusion dominates recovery times for larger droplets. Green circle: FRAP recovery time obtained from direct simulation of an A6B6 droplet of radius 37 nm. Black curve: the recovery time as a function of droplet radius from a single exponential fit of the exact solution of the recovery curve from Equations (1) - (4). Gray curve: the recovery time predicted by Equation (6). Yellow, blue, and red curves: the recovery time when dense-phase, dilute-phase, and interface flux limit the exchange dynamics, i.e., the first, second, and last term in Equation (6), respectively. Parameters matched to the simulated A6B6 system in the slab geometry: (B) Time courses of fluorescence profiles for A6B6 droplets of radius  (top) and  (bottom); red is fully bleached, green is fully recovered. These concentration profiles are the numerical solutions of Equations (1) - (3) using the parameters in (A). (Below Figure 5)”

Author response:

We thank the reviewers for their insightful comments on our model and manuscript. In this provisional response, we would like to comment on some of the issues raised and how we plan to address them.

First, the reviewers correctly pointed out that only a small part of the full model was openly available. We have now rectified this and the full model is available at: https://dataverse.harvard.edu/dataverse/sscx.

Next, we would like to comment on the perceived lack of clarity of certain descriptions in the manuscript. We note that individual techniques and parts of the model have been developed, justified, and validated in previous publications. This left us with the question of how much of the contents of those papers we should re-describe. Too much, and the manuscript becomes overly long; too little, and the reader cannot gain a sufficient understanding of the model building process. The reviewers' comments made it clear that some aspects of the model should be described in more detail and we plan to address this in a revision. Crucially, one missing item raised by all reviewers was a comparison of local connection probabilities to the literature. This will be provided in the revision. Additionally, the reviewers questioned our decision to use a connectivity algorithm that is not based on direct parameterization of target connection probabilities. While this is a limitation of the algorithm we employed, it also has unique strengths, providing non-random aspects of connectivity that have been proven to be impossible to model with algorithms that enforce given connection probabilities or degree distributions. We plan to explain this better in a revision.

We will also comment on the challenges associated with the interpretation of experimentally measured connection probabilities and employing them for the parameterization of a biophysically detailed model spanning millimeters.

The reviewers also suggested several aspects of the model that could be improved. Whilst we see merit with all of them, we would like to briefly comment on model completeness in general. First, this model - and any model - can probably never be considered complete. Instead, the model has to be continuously refined, which one reviewer phrased as the "live nature" of the model. However, to demonstrate the model's utility and justify the expense of modeling, we also have to use the model in projects that explore specific scientific questions. To undertake and complete such a project, one must select and "freeze" a given version of the model-- otherwise the project will never conclude. Further, we believe that it is advantageous if several projects use the same version of the model. In that case, a reader who is already familiar with the model from one paper may find it easier to understand other papers using the same model. The goal of this manuscript is to describe the version of the model that we used in several ongoing and concluded follow-up projects, including its limitations and opportunities for refinement. As such, we do not plan to add further improvements to the model for this reviewed pre-print. We will, however, continue to refine the model outside of the scope of this publication. Since we believe the development and bottom up models are best done in a community driven manner, we encourage interested parties to participate.

We invite anyone with ideas of how the model could be refined to contact us to discuss how we could integrate these changes into the model together using our tools.

Author response:

eLife assessment

This important study reports numerous attempts to replicate reports on transgenerational inheritance of a learned behavior, pathogen avoidance, in C. elegans. While the authors observe parental effects that are limited to a single generation (also called intergenerational inheritance), the authors failed to find any evidence for transmission over multiple generations, or transgenerational inheritance. The experiments presented are meticulously described, making for compelling evidence that in the authors' hands transgenerational inheritance cannot be observed, although there remains the possibility that subtle differences in culture conditions or lab environment explain the failure to reproduce previous observations. Given the prominence of the original reports of transgenerational inheritance, the present study is of broad interest to anyone studying genetics, epigenetics, or learned behavior.

Thank you for your considered reviews and advice on how to improve our manuscript. We appreciate that the editors and reviewers felt that our manuscript addressed an important issue and acknowledged the difficulty of publishing negative results. We will revise the manuscript and consider all the concerns raised by the editor and referees.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors report an inability to reproduce a transgenerational memory of avoidance of the pathogen PA14 in C. elegans. Instead, the authors demonstrate intergenerational inheritance for a single F1 generation, in embryos of mothers exposed to OP50 and PA14, where embryos isolated from these mothers by bleaching are capable of remembering to avoid PA14 in a manner that is dependent on systemic RNAi proteins sid-1 and sid-2. This could reflect systemic sRNAs generated by neuronal daf-7 signaling that are transmitted to F1 embryos. The authors note that transgenerational memory of PA14 was reported by the Murphy group at Princeton, but that environmental or strain variation (worms or bacteria) might explain the single generation of inheritance observed at Harvard. The Hunter group tried different bacterial growth conditions and different worm growth temperatures for independent PA14 strains, which they showed to be strongly pathogenic. However, the authors could not reproduce a transgenerational effect at Harvard. This important data will allow members of the scientific community to focus on the robust and reproducible inheritance of PA14 avoidance transmitted to F1 embryos of mothers exposed to PA14, which the authors demonstrate depends on small RNAs in a manner that is downstream of or in parallel to daf-7. This paper honestly and importantly alters expectations and questions the model that avoidance of PA14 is mediated by a bacterial ncRNA whose siRNAs target a C. elegans gene. Instead, endogenous C. elegans sRNAs that affect pathogen response may be the culprit that explains sRNA-mediated avoidance.

Overall, this is an important paper that demonstrates that one model for transgenerational inheritance in C. elegans is not reproducible. This is important because it is not clear how many of the reported models of transgenerational inheritance reported in C. elegans are reproducible. The authors do demonstrate a memory for F1 embryos that could be a maternal effect, and the authors confirm that this is mediated by a systemic small RNA response. There are several points in the manuscript where a more positive tone might be helpful.

We would like to correct the statement made in the second to last sentence. The demonstration of an F1 response to PA14 was first reported by Moore et al., (2019) and then by Pereira et al., (2020) using a different behavioral assay. We merely confirmed these results in our hands, and confirmed the observation, first reported by Kaletsky et al., (2020), that sid-1 and sid-2 are required for this F1 response; although we did find that sid-1 and sid-2 are not required for the PA14-induced increase in daf-7p::gfp expression in ASI neurons in the F1 progeny of trained adults, which had not been addressed in the published work.

Yes, the intergenerational F1 response could be a maternal effect, but the in utero F1 embryos and their precursor germ cells were directly exposed to PA14 metabolites and toxins (non-maternal effect) as well as any parental response, whether mediated by small RNAs, prions,  hormones, or other unknown information carriers. While the F1 aversion response does require sid-1 and sid-2, we would not presume that the substrate is therefore an RNA molecule, particularly because the systemic RNAi response supported by sid-1 and sid-2 is via long double-stranded RNA. To date, no evidence suggests that either protein transports small RNAs, particularly single-stranded RNAs. 

Strengths:

The authors note that the high copy number daf-7::GFP transgene used by the Murphy group displayed variable expression and evidence for somatic silencing or transgene breakdown in the Hunter lab, as confirmed by the Murphy group. The authors nicely use single copy daf-7::GFP to show that neuronal daf-7::GFP is elevated in F1 but not F2 progeny with regards to the memory of PA14 avoidance, speaking to an intergenerational phenotype.

The authors nicely confirm that sid-1 and sid-2 are generally required for intergenerational avoidance of F1 embryos of moms exposed to PA14. However, these small RNA proteins did not affect daf-7::GFP elevation in the F1 progeny. This result is unexpected given previous reports that single copy daf-7::GFP is not elevated in F1 progeny of sid mutants. Because the Murphy group reported that daf-7 mutation abolishes avoidance for F1 progeny, this means that the sid genes function downstream of daf-7 or in parallel, rather than upstream as previously suggested.

The authors studied antisense small RNAs that change in Murphy data sets, identifying 116 mRNAs that might be regulated by sRNAs in response to PA14. Importantly, the authors show that the maco-1 gene, putatively targeted by piRNAs according to the Kaletsky 2020 paper, displays few siRNAs that change in response to PA14. The authors conclude that the P11 ncRNA of PA14, which was proposed to promote interkingdom RNA communication by the Murphy group, is unlikely to affect maco-1 expression by generating sRNAs that target maco-1 in C. elegans. The authors define 8 genes based on their analysis of sRNAs and mRNAs that might promote resistance to PA14, but they do not further characterize these genes' role in pathogen avoidance. The Murphy group might wish to consider following up on these genes and their possible relationship with P11.

Weaknesses:

This very thorough and interesting manuscript is at times pugnacious.

We reiterate that we never claimed that Moore et al., (2019) did not obtain their reported results. We simply stated that we could not replicate their results using the published methods and then failed in our search to identify variable(s) that might account for our results. We will do better when revising the manuscript to make clear, unmuddied statements of facts and state that future investigations may provide independent evidence that supports the original claims and explains our divergent results.

Please explain more clearly what is High Growth media for E. coli in the text and methods, conveying why it was used by the Murphy lab, and if Normal Growth or High Growth is better for intergenerational heritability assays.

We used the standard recipes as described in Moore et al., (2021), and will include the recipes and some of the relevant commentary from the paragraphs below to the methods and text as appropriate. 

Normal Growth (NG) media minimally supports OP50 growth, resulting in a thin lawn that minimally obscures viewing larvae and embryos. High Growth (HG) media contains 8X more peptone, which supports much higher OP50 growth, resulting in a thick bacterial lawn that supports larger worm populations. The thicker bacterial lawn can also compromise agar integrity, and the higher worm density encourages worm burrowing behavior, thus the HG plates also have 75% more agar to inhibit worm burrowing. 

Our results (Figure 4) show that worms grown on OP50 seeded NG or HG plates show different choice responses (PA14 vs OP50). As for experimental “advice”, we would caution our colleagues to not assume that OP50 is a neutral food and to be aware that how you grow and store OP50 (or any bacterial culture that is to be used as food for worms) may have a significant effect on the phenotype you are studying. 

Reviewer #2 (Public Review):

This paper examines the reproducibility of results reported by the Murphy lab regarding transgenerational inheritance of a learned avoidance behavior in C. elegans. It has been well established by multiple labs that worms can learn to avoid the pathogen pseudomonas aeruginosa (PA14) after a single exposure. The Murphy lab has reported that learned avoidance is transmittable to 4 generations and dependent on a small RNA expressed by PA14 that elicits the transgenerational silencing of a gene in C. elegans. The Hunter lab now reports that although they can reproduce inheritance of the learned behavior by the first generation (F1), they cannot reproduce inheritance in subsequent generations.

This is an important study that will be useful for the community. Although they fail to identify a "smoking gun", the study examines several possible sources for the discrepancy, and their findings will be useful to others interested in using these assays. The preference assay appears to work in their hands in as much as they are able to detect the learned behavior in the P0 and F1 generations, suggesting that the failure to reproduce the transgenerational effect is not due to trivial mistakes in the protocol. An obvious reason, however, to account for the differing results is that the culture conditions used by the authors are not permissive for the expression of the small RNA by PA14 that the MUrphy lab identified as required for transgenerational inheritance. It would seem prudent for the authors to determine whether this small RNA is present in their cultures, or at least acknowledge this possibility.

We note that Kaletsky et al., (2020) (Figure 3L) showed that PA14 ΔP11 bacteria failed to induce an F1 avoidance response. Thus, the fact that we observed F1 avoidance implies that our culture conditions successfully induced P11 expression. We believe that this addresses the concern raised here. We thank the reviewer for raising this issue and we will add a statement to this effect in the revised manuscript.

The authors should also note that their protocol was significantly different from the Murphy protocol (see comments below) and therefore it remains possible that protocol differences cumulatively account for the different results.

We disagree. Our adjustments to the core protocol were minor and, where possible, were explicitly tested in side-by-side experiments. To discover the source(s) of discrepancy between our results and the published results we subsequently introduced variations to this core protocol to exclude likely variables (worm and bacteria growth temperatures, assay conditions, worm handling methods, bacterial culture and storage conditions, and some minor developmental timing issues). To substantiate these assertions, we will, upon revision, add the precise protocol we followed for the aversion assay to the supplemental documents, provide some additional experimental results supporting these claims, and further clarify which presented experiments included protocol variations (e.g. sodium azide or cold immobilization). It remains possible that we misunderstood the published protocol, but we were highly motivated to replicate the results and read every published version with extreme care.

Reviewer #3 (Public Review):

Summary:

It has been previously reported in many high-profile papers, that C. elegans can learn to avoid pathogens. Moreover, this learned pathogen avoidance can be passed on to future generations - up to the F5 generation in some reports. In this paper, Gainey et al. set out to replicate these findings. They successfully replicated pathogen avoidance in the exposed animals, as well as a strong increase in daf-7 expression in ASI neurons in F1 animals, as determined by a daf-7::GFP reporter construct. However, they failed to see strong evidence for pathogen avoidance or daf-7 overexpression in the F2 generation. The failure of replication is the major focus of this work.

Given their failure to replicate these findings, the authors embark on a thorough test of various experimental confounders that may have impacted their results. They also re-analyze the small RNA sequencing and mRNA sequencing data from one of the previously published papers and draw some new conclusions, extending this analysis.

Strengths:

(1) The authors provide a thorough description of their methods, and a marked-up version of a published protocol that describes how they adapted the protocol to their lab conditions. It should be easy to replicate the experiments.

(2) The authors test the source of bacteria, growth temperature (of both C. elegans and bacteria), and light/dark husbandry conditions. They also supply all their raw data, so that the sample size for each testing plate can be easily seen (in the supplementary data). None of these variations appears to have a measurable effect on pathogen avoidance in the F2 generation, with all but one of the experiments failing to exhibit learned pathogen avoidance.

(3) The small RNA seq and mRNA seq analysis is well performed and extends the results shown in the original paper. The original paper did not give many details of the small RNA analysis, which was an oversight. Although not a major focus of this paper, it is a worthwhile extension of the previous work.

(4) It is rare that negative results such as these are accessible. Although the authors were unable to determine the reason that their results differ from those previously published, it is important to document these attempts in detail, as has been done here. Behavioral assays are notoriously difficult to perform and public discourse around these attempts may give clarity to the difficulties faced by a controversial field.

Thank you for your support. Choosing to pursue publication of these negative results was not an easy decision, and we thank members of the community for their support and encouragement.

Weaknesses:

(1) Although the "standard" conditions have been tested over multiple biological replicates, many of the potential confounders that may have altered the results have been tested only once or twice. For example, changing the incubation temperature to 25{degree sign}C was tested in only two biological replicates (Exp 5.1 and 5.2) - and one of these experiments actually resulted in apparent pathogen avoidance inheritance in the F2 generation (but not in the F1). An alternative pathogen source was tested in only one biological replicate (Exp 3). Given the variability observed in the F2 generation, increasing biological replicates would have added to the strengths of the report.

We agree that our study was not exhaustive in our exploration of variables that might be interfering with our ability to detect F2 avoidance. We also note that some of these variables also failed (with many more independent experiments) to induce elevated daf-7p::gfp expression in ASI neurons in F2 progeny. Our goal was not to show that variation in some growth or assay condition would generate reproducible negative results, the exploration was designed to tweak conditions to enable detection of a robust F2 response. Given the strength of the data presented in Moore et al., (2019) we expected that adjustment of the problematic variable would produce positive results apparent in a single replicate, which could then be followed up. If we had succeeded, then we would have documented the conditions that enabled robust F2 inheritance and would have explored molecular mechanisms that support this important but mysterious process.

(2) A key difference between the methods used here and those published previously, is an increase in the age of the animals used for training - from mostly L4 to mostly young adults. I was unable to find a clear example of an experiment when these two conditions were compared, although the authors state that it made no difference to their results.

We can state firmly that the apparent time delay did not affect P0 learned avoidance or, as documented in Table S1, daf-7p::gfp expression in ASI neurons. In our experience, training mostly L4’s on PA14 frequently failed to produce sufficient F1 embryos for both F1 avoidance assays or daf-7p::gfp measurements in ASI neurons and collection of F2 progeny. Indeed, in early attempts to detect heritable PA14 aversion, trained P0 and F1 progeny were not assayed in order to obtain sufficient F2’s for a choice assay. These animals failed to display aversion, but without evidence of successful P0 training or an F1 intergenerational response this was deemed a non-fruitful trouble-shooting approach. We will add to our supplemental figures P0 choice results from experiments using younger trained animals that failed to produce sufficient F1’s to continue the inheritance experiments. 

The different timing between the two protocols may reflect the age of the recovered bleached P0 embryos. It is reasonable to assume that bleaching day 1 adults vs day 2 adults from the P-1 population could shift the average age of recovered P0 embryos by several hours. The Murphy protocol only states that P0 embryos were obtained by bleaching healthy adults. Regardless, if the hypothesis entertained here is true, that a several hour difference in larval/adult age during 24 hours of training affects F2 inheritance of learned aversion but does not affect P0 learned avoidance, then we would argue that this paradigm for heritable learned avoidance, as described in Moore et al, (2019, 2021), is not sufficiently robust for mechanistic investigations. 

(3) The original paper reports a transgenerational avoidance effect up to the F5 generation. Although in this work the authors failed to see avoidance in the F2 generation, it would have been prudent to extend their tests for more generations in at least a couple of their experiments to ensure that the F2 generation was not an aberration (although this reviewer acknowledges that this seems unlikely to be the case).

Citations

Moore, R.S., Kaletsky, R., and Murphy, C.T. (2019). Piwi/PRG-1 Argonaute and TGF-beta Mediate Transgenerational Learned Pathogenic Avoidance. Cell 177, 1827-1841 e1812.

Pereira, A.G., Gracida, X., Kagias, K., and Zhang, Y. (2020). C. elegans aversive olfactory learning generates diverse intergenerational effects. J Neurogenet 34, 378-388.

Kaletsky, R., Moore, R.S., Vrla, G.D., Parsons, L.R., Gitai, Z., and Murphy, C.T. (2020). C. elegans interprets bacterial non-coding RNAs to learn pathogenic avoidance. Nature 586, 445-451.

Moore, R.S., Kaletsky, R., and Murphy, C.T. (2021). Protocol for transgenerational learned pathogen avoidance behavior assays in Caenorhabditis elegans. STAR Protoc 2, 100384.

Author response:

We appreciate the time and effort that you and the reviewers have dedicated to providing valuable feedback on our manuscript. We are grateful to the reviewers for their insightful comments.

Reviewer #1:<br /> We thank the reviewer for the positive comments made on our manuscript.

Reviewer #2:<br /> We thank the reviewer for these positive remarks.

Concerning the main weakness highlighted by the reviewer:

We presented results in our submitted work both without noise and with a signal-to-noise ratio (SNR) equal to 50. Figure 5 shows exemplar posterior distributions obtained in a noise-free scenario, and Table 1 reports the number of degeneracies for each model on 10000 noise-free simulations. These results highlight that the presence of degeneracies is inherent to the model definition. Figures 3, 6 and 7 present results considering an SNR of 50. Results with lower SNR have indeed not been included into this work. We agree that adding a figure showing the impact of noise on the posterior distributions will be a good addition to this work. We will include an additional figure in the second version, as interestingly suggested.

Author response:

Reviewer #1 (Recommendations For The Authors):

(1) Figure 3B was not cited in the manuscript.

We have now included the citation for Figure 3B in the main text: “….whereas NSP13-R567A (lost ATP consumption) and NSP13-K345A/K347A (obstructed the nucleic acid binding channel) failed to inhibit YAP activity (Figure 3B).” (Please see the revised manuscript) 

Reviewer #2 (Recommendations For The Authors):

(2) In Figure 1, ciliated cells are marked as a separate cluster from "epithelial cells". Since ciliated cells are epithelial cells, I suggest changing the nomenclature of the clusters.

We have updated the label from “Ciliated” to “Ciliated Epithelial” in Figure 1A, as suggested. (Please see the revised manuscript)

(3) Outlines of planned revisions: 1) Reanalyze snRNA-seq and bulk RNA-seq data from Figure 1 to investigate YAP target genes related to innate immune response; 2) Employ ChIP-seq to determine whether NSP13 WT or mutants (K131, K345/K347, and R567) prevent YAP/TEAD complex from binding to DNA by occupying the TEAD DNA binding site, providing insights into the mechanism; 3) Validate NSP13 interacting proteins using Immunoprecipitation-Western Blot (IP-WB) assays based on mass spectrum results; 4) Perform bulk RNA sequencing in cells with or without NSP13 expression to assess endogenous YAP target genes expression.

Author response:

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

Reviewer #1 (Public Review):

Overall the authors provide a very limited data set and in fact only a proof of concept that their sensor can be applied in vivo. This is not really a research paper, but a technical note. With respect to their observation of clustered activity, they now provide an overview image, next to zoomed details. However, from these images one cannot conclude 'by eye' any clustering event. This aligns with the very low r values. All neurons in the field show variable activity and a clustering is not really evident from these examples. Even within a cluster, there is variability. The authors now confirm that expression levels are indeed variable but are independent from the ratio measurements. Further, they controlled for specificity by including DAPT treatments, but opposite to their own in vitro data (in primary neurons) the ratios increased. The authors argue that both distance and orientation can either decrease or increase ratios and that the use of this biosensor should be explored model-by-model. This doesn't really confer high confidence and may hinder other groups in using this sensor reliably.

Secondly, there is still no physiological relevance for this observation. The experiments are performed in wild-type mice, but it would be more relevant to compare this with a fadPSEN1 KI or a PSEN1cKO model to investigate the contribution of a gain of toxic function or LOF to the claimed cell non-autonomous activations. The authors acknowledge this shortcoming but argue that this is for a follow-up study.

For instance, they only monitor activity in cell bodies, and miss all info on g-sec activity in neurites and synapses: what is the relevance of the cell body associated g-sec and can it be used as a proxy for neuronal g-sec activity? If cells 'communicate' g-sec activities, I would expect to see hot spots of activity at synapses between neurons.

Without some more validation and physiologically relevant studies, it remains a single observation and rather a technical note paper, instead of a true research paper.

The effect size was small, as stated in the original and revised manuscripts and the point-by-point responses to the 1st round review. Such subtle effects will likely be challenging to detect by eye. However, our unbiased quantification allowed us to detect a statistically significant linear correlation between the 720/670 ratio in each neuron and the average ratio in neighboring neurons, which we have verified using many different approaches (Figure 3, Figure 3—figure supplement 2, and Figure 4), and the correlation was canceled by the administration of g-secretase inhibitor (Figure 5). Such objective analysis made us more confident to conclude that g-secretase affects g-secretase in neighboring neurons.

We would also like to make clear the design of the C99 720-670 biosensor. Both C99, the sensing domain that is cleaved by g-secretase, and the anchoring domain fused to miRFP670 are integrated into the membrane (Figure 1A). Therefore, how these two domains with four transmembrane regions are embedded in the membrane should affect the orientation between the donor, miRFP670, and the acceptor, miRFP720. As noted in our point-by-point responses to the initial review, we have previously validated that pharmacological inhibition of g-secretase significantly increases the FRET ratio in various cell lines, including CHO, MEF, BV2 cells, and mouse cortical primary neurons (Maesako et al., 2020; Houser et al., 2020, and unpublished observations). On the other hand, FRET reduction by g-secretase inhibition was found in mouse primary neurons derived from the cerebellum (unpublished observations) as well as the somatosensory cortex neurons in vivo (this study). While we could not use the exact same imaging set-up between cortical primary neurons in vitro and those in vivo due to different expression levels of the biosensor, we could do it for in vitro cortical primary neurons vs. in vitro cerebellum neurons. We found by the direct comparison that 720/670 ratios are significantly higher in the cerebellum than the cortex neurons even in the presence of 1 mM DAPT (Author response image 1), a concentration that nearly completely inhibits g-secretase activity. This suggests a different integration and stabilization pattern of the sensing and anchoring domains in the C99 720-670 biosensor between the cortex and cerebellum primary neurons, and thus, orientation between the donor and acceptor varies in the two neuronal types. We expect a similar scenario between cortical primary neurons in vitro and those in vivo. Of note, we have recently demonstrated that the cortex and cerebellum primary neurons exhibit distinct membrane properties (Lundin and Wieckiewicz et al., 2024 in revision), suggesting the different baseline FRET could be related to the different membrane properties between the cortex and cerebellum primary neurons. On the other hand, this raises a concern that 720/670 ratios can be affected not only by g-secretase activity but also by other cofounders, such as altered membrane properties. However, a small but significant correlation between the 720/670 ratio in a neuron and those ratios in its neighboring neurons is canceled by g-secretase inhibitor (Figure 5), suggesting that the correlation between the 720/670 ratio in a neuron and those in its neighboring neurons is most likely dependent on g-secretase activity. Taken together, we currently think orientation plays a significant role in our biosensor and would like to emphasize the importance of ensuring on a model-by-model basis whether the cleavage of the C99 720-670 biosensor by g-secretase increases or decreases 720/670 FRET ratios.

Author response image 1.

Furthermore, we co-expressed the C99 720-670 biosensor and visible range fluorescence reporters to record other biological events, such as changes in ion concentration, in cortex primary neurons. Interestingly, several biological events uniquely detected in the neurons with higher 720/670 ratios, which are expected to exhibit lower endogenous g-secretase activity, are recapitulated by pharmacological inhibition of g-secretase (unpublished observations), ensuring that higher 720/670 ratios are indicative of lower g-secretase activity in mouse cortex primary neurons. Such multiplexed imaging will help to further elucidate how the C99 720-670 biosensor behaves in response to the modulation of g-secretase activity.

Lastly, the scope of this study was to develop and validate a novel imaging assay employing a NIR FRET biosensor to measure g-secretase activity on a cell-by-cell basis in live wild-type mouse brains. However, we do appreciate the reviewer’s suggestion and think employing this new platform in FAD PSEN1 knock-in (KI) or PSEN1 conditional knockout (cKO) mice would provide valuable information. Furthermore, we are keen to expand our capability to monitor g-secretase with subcellular resolution in live mouse brains in vivo, which we will explore in follow-up studies. Thank you for your thoughtful suggestions.

Reference

- Maesako M, Sekula NM, Aristarkhova A, Feschenko P, Anderson LC, Berezovska O. Visualization of PS/γ-Secretase Activity in Living Cells. iScience. 2020 Jun 26;23(6):101139.

- Houser MC, Hou SS, Perrin F, Turchyna Y, Bacskai BJ, Berezovska O, Maesako M. A Novel NIR-FRET Biosensor for Reporting PS/γ-Secretase Activity in Live Cells. Sensors (Basel). 2020 Oct 22;20(21):5980.

- Lundin B, Wieckiewicz N, Dickson JR, Sobolewski RGR, Sadek M, Armagan G, Perrin F, Hyman BT, Berezovska O, and Maesako M. APP is a regulator of endo-lysosomal membrane permeability. 2024 in revision

Reviewer #2 (Public Review):

Regarding the variability and spatial correlation- the dynamic range of the sensor previously reported in vitro is in the range of 20-30% change (Houser et al 2020) whereas the range of FR detected in vivo is between cells is significantly larger in this MS. This raises considerable doubts for specific detection of cellular activity.

One direct way to test the dynamic range of the sensor in vivo, is to increase or decrease endogenous gamma-secretase activity and to ensure this experimental design allows to accurately monitor gamma-secretase activity. In the previous characterization of the reporter (Hauser et al 2020), DAPT application and inhibition of gamma-secretase activity results in increased FR (Figures 2 and 3 of Houser et al). This is in agreement with the design of the biosensor, since FR should be inversely correlated with enzymatic activity. Here, the authors repeated the experiment, and surprisingly found an opposite effect, in which DAPT significantly reduced FR.

The authors maintain that this result could be due to differences in cell-types, However, this experiment was previously performed in cultures cortical neurons and many different cell types, as noted by the authors in their rebuttal.

Instead, I would argue that these results further highlight the concerns of using FR in vivo, since based on their own data, there is no way to interpret this quantification. If DAPT reduces FR, does this mean we should now interpret the results of higher FR corresponds to higher g-sec activity? Given a number of papers from the authors claiming otherwise, I do not understand how one can interpret the results as indicating a cell-specific effect.

In conclusion, without any ground truth, it is impossible to assess and interpret what FR measurements of this sensor in vivo mean. Therefore, the use of this approach as a way to study g-sec activity in vivo seems premature.

Please find our response to reviewer 1’s similar critique above. Here, we again would like to re-clarify the design of our C99 720-670 biosensor. The orientation between the donor, miRFP670, and acceptor, miRFP720, is dependent on how C99, the sensing domain that is cleaved by g-secretase, and the anchoring domain are integrated into the membrane (Figure 1A). Although it was surprising to us, it is possible that g-secretase inhibition decreases 720/670 ratios if 1) the donor-acceptor orientation plays a significant role in FRET and 2) the baseline structure of the C99 720-670 biosensor is different between cell types. This appears to be the case between the cortex and cerebellum primary neurons (i.e., DAPT increases 720/670 ratios in the cortex neurons while decreasing in the cerebellum neurons), and we expect it in cortical neurons in vitro vs. in vivo as well. Hence, we recommend that users first validate whether the cleavage of the C99 720-670 biosensor by g-secretase increases or decreases 720/670 FRET ratios in their models. If DAPT increases 720/670 ratios (like in cortex primary neurons, CHO, MEF, and BV2 cells that we have validated), the results of higher ratios should be interpreted as lower g-secretase activity. If DAPT reduces 720/670 ratios (like in cerebellum primary neurons and the somatosensory cortex neurons in vivo), we should interpret the results of higher ratios corresponding to higher g-secretase activity. From a biosensing perspective, although we need to know which is the case on a model-by-model basis, we think whether g-secretase activity increases or decreases the 720/670 ratio is not critical; rather, if it can significantly change FRET efficiency is more important. Thank you for your critical comments.

Reviewer #3 (Public Review):

This paper builds on the authors' original development of a near infrared (NIR) FRET sensor by reporting in vivo real-time measurements for gamma-secretase activity in the mouse cortex. The in vivo application of the sensor using state-of-the-art techniques is supported by a clear description and straightforward data, and the project represents significant progress because so few biosensors work in vivo. Notably, the NIR biosensor is detectable to ~ 100 µm depth in the cortex. A minor limitation is that this sensor has a relatively modest ΔF as reported in Houser et al, which is an additional challenge for its use in vivo. Thus, the data is fully dependent on post-capture processing and computational analyses. This can unintentionally introduce biases but is not an insurmountable issue with the proper controls that the authors have performed here.

The following opportunity for improving the system didn't initially present itself until the authors performed an important test of the FRET sensor in vivo following DAPT treatment. The authors get credit for diligently reporting the unexpected decrease in 720/670 FRET ratio. In turn this has led to a suggestion that this sensor would benefit from a control that is insensitive to gamma-secretase activity. FRET influences that are independent of gamma-secretase activity could be distinguished by this control.

From previous results in cultured neurons, the authors expected an increase in FRET following DAPT treatment in vivo. These expectations fit with the sensor's mode-of-action because a block of gamma-secretase activity should retain the fluorophores in proximity. When the authors observed decreased FRET, the conclusion was that the sensor performs differently in different cellular contexts. However, a major concern is that mechanistically it is unclear how this could occur with this type of sensor. The relative orientation of fluorophores indeed can contribute to FRET efficiency in tension-based sensors. However, the proteolysis expected with gamma-secretase activity would release tension and orientation constraints. Thus, the major contributing FRET factor is expected to be distance, not orientation. Alternative possibilities that could inadvertently affect readouts include an additional DAPT target in vivo sequestering the inhibitor, secondary pH effects on FRET, photo-bleaching, or an unidentified fluorophore quencher in vivo stimulated by DAPT. Ultimately this new FRET sensor would benefit from a control that is insensitive to gamma-secretase activity. FRET influences that are independent of gamma-secretase activity could be distinguished by this control.

Given that the anchoring domain is composed of three transmembrane regions and the linker connecting the donor, miRFP670, and the acceptor, miRFP720, is highly flexibility, we are still not sure if the orientation constraint of the C99 720-670 biosensor is canceled by g-secretase cleavage. This means that the orientation between the donor and acceptor in the cleaved form of the sensor can be different between model and model. As explained in response to the similar critique of reviewer 1, we found that the 720/670 ratio is significantly higher in the cerebellum than in the cortex neurons even in the presence of DAPT (Figure 1 for the review only). Therefore, we currently think the donor-acceptor orientation, both in the cleaved and non-cleaved forms of the sensor, plays a role in determining whether g-secretase activity increases or decreases the 720/670 ratio (but this view may change depends on the future discoveries).

As the reviewer pointed out, the NIR g-secretase biosensor with no biological activity is important; however, a point mutation in the transmembrane region of the C99 sensing domain could also result in altered orientation between the donor, miRFP670, and the acceptor, miRFP720, since C99 is connected to the acceptor, which may bring additional complexity. Also, as noted in our point-by-point responses to the initial review, the mutation(s) that can fully block C99 processing by g-secretase has not been established. Therefore, we asked if a subtle but significant correlation we found between the 720/670 ratio in a neuron and those ratios in its neighboring neurons is canceled by g-secretase inhibitor administration. Since the correlation was abolished (Figure 5), it suggests that the correlation between the 720/670 ratio in a neuron and those ratios in the neighboring neurons depends on g-secretase activity.

It is not fully established how g-secretase activity is spatiotemporally regulated; therefore, the development of more appropriate control biosensors and further validation of our findings with complementary approaches would be crucial in our follow-up studies. Thank you for your valuable comments.

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

Reviewer #1 (Public Review):

(1) Overall the authors provide a very limited data set and in fact only a proof of concept that their sensor can be applied in vivo. This is not really a research paper, but a technical note. With respect to their observation of clustered activity, the images do not convince me as they show only limited areas of interest: from these examples (for instance fig 5) one sees that merely all neurons in the field show variable activity and a clustering is not really evident from these examples. Even within a cluster, there is variability. With r values between 0.23 to .36, the correlation is not that striking. The authors herein do not control for expression levels of the sensor: for instance, can they show that in all neurons in the field, the sensor is equally expressed, but FRET activity is correlated in sets of neurons? Or are the FRET activities that are measured only in positively transduced neurons, while neighboring neurons are not expressing the sensor? Without such validation, it is difficult to make this conclusion.

We appreciate the reviewer’s comment. We agree with the reviewer that this study is not testing a new hypothesis but rather developing and validating a novel tool. However, we do believe such a “technical note” is as important as a “research paper” since advancing technique(s) is the only way to break the barrier in our understanding of complex biological events. Therefore, this study aimed to develop and validate a novel imaging assay employing a recently engineered NIR FRET biosensor to measure γ-secretase activity (Houser et al., 2020) on a cell-by-cell basis in live mouse brains, enabling us for the first time to examine how γ-secretase activity is regulated in individual neurons in vivo, and uncover that γ-secretase activity may influence γ-secretase in neighboring neurons. Like the reviewer, we found that the cell-to-cell correlation is not that striking, as we clearly stated in the original manuscript: “Although the effect size is modest, we also found a statistically significant correlation between…” 

We were also aware that there is variability in a cluster of neurons exhibiting similar γ-secretase activities. Per the reviewer’s request, the images have been expanded to the entire imaging field of view (new Figure 3A). Although the effect size is small, our unbiased quantification showed a statistically significant linear correlation between the 720/670 ratio in each neuron and the average ratio in five neighboring neurons (Figure 3, Figure 3—figure supplement 2, and Figure 4), and the correlation was canceled by the administration of γ-secretase inhibitor (Figure 5). These findings made it impossible to conclude that γ-secretase does not affect γ-secretase in neighboring neurons.

Regarding the expression levels and pattern of the sensor, an AAV-based gene delivery approach employed in this study results in the expression of the sensor not in all but in selected neurons. We have newly performed immunohistochemistry, showing that approximately 40% of NeuN-positive neurons express the C99 720-670 biosensor (new Figure 1—figure supplement 2A and 2B).

Reference

- Houser MC, Hou SS, Perrin F, Turchyna Y, Bacskai BJ, Berezovska O, Maesako M. A Novel NIRFRET Biosensor for Reporting PS/γ-Secretase Activity in Live Cells. Sensors (Basel). 2020 Oct 22;20(21):5980. 

(2) Secondly, I am lacking some more physiological relevance for this observation. The experiments are performed in wild-type mice, but it would be more relevant to compare this with a fadPSEN1 KI or a PSEN1cKO model to investigate the contribution of a gain of toxic function or LOF to the claimed cell non-autonomous activations. Or what would be the outcome if the sensor was targeted to glial cells?

The AAV vector in this study encodes the human synapsin promoter and our new immunohistochemistry demonstrates that nearly 100% of the cells expressing the C99 720-670 sensor are NeuN positive, and we hardly detected the sensor expression in Iba-1 or GFAP-positive cells (new Figure 1— figure supplement 2A and 2C). 

The mechanism underlying the cell non-autonomous regulation of γ-secretase remains unclear. As discussed in our manuscript, one of the potential hypotheses could be that secreted abeta42 plays a role (Zoltowska et al., 2023 eLife). Whereas this report focuses on the development and validation of a novel assay using wildtype mice, future follow-up studies employing FAD PSEN1 knock-in (KI) and PSEN1 conditional knockout (cKO) mice would allow us test the hypothesis above since abeta42 is known to increase in some FAD PSEN1 KI mice (Siman et al., 2000 J Neurosci, Vidal et al., 2012 FASEB J) while decreases in PSEN1 cKO mice (Yu et al., 2001 Neuron).  

Reference

- Siman R, Reaume AG, Savage MJ, Trusko S, Lin YG, Scott RW, Flood DG. Presenilin-1 P264L knockin mutation: differential effects on abeta production, amyloid deposition, and neuronal vulnerability. J Neurosci. 2000 Dec 1;20(23):8717-26. 

- Vidal R, Sammeta N, Garringer HJ, Sambamurti K, Miravalle L, Lamb BT, Ghetti B. The Psen1-L166Pknock-in mutation leads to amyloid deposition in human wild-type amyloid precursor protein YAC transgenic mice. FASEB J. 2012 Jul;26(7):2899-910. 

- Yu H, Saura CA, Choi SY, Sun LD, Yang X, Handler M, Kawarabayashi T, Younkin L, Fedeles B, Wilson MA, Younkin S, Kandel ER, Kirkwood A, Shen J. APP processing and synaptic plasticity in presenilin-1 conditional knockout mice. Neuron. 2001 Sep 13;31(5):713-26. 

- Zoltowska KM, Das U, Lismont S, Enzlein T, Maesako M, Houser MC, Franco ML, Moreira DG, Karachentsev D, Becker A, Hopf C, Vilar M, Berezovska O, Mobley W, Chávez-Gutiérrez L. Alzheimer's disease linked Aβ42 exerts product feedback inhibition on γ-secretase impairing downstream cell signaling. eLife. 2023. 12:RP90690

(3) For this reviewer it is not clear what resolution they are measuring activity, at cellular or subcellular level? In other words are the intensity spots neuronal cell bodies? Given g-sec activity are in all endosomal compartments and at the cell surface, including in the synapse, does NIR imaging have the resolution to distinguish subcellular or surface localized activities? If cells 'communicate' g-sec activities, I would expect to see hot spots of activity at synapses between neurons: is this possible to assess with the current setup? 

Since this study aimed to determine how γ-secretase activity is regulated on a cell-by-cell basis in live mouse brains, the FRET signal was detected in neuronal cell bodies. While our current set-up for in vivo can only record γ-secretase activity with a cellular resolution, we previously detected predominant γ-secretase activity in the endo-lysosomal compartments (Maesako et al., 2022 J Neurosci) as well as in certain spots of neuronal processes (Maesako et al., 2020 iScience) in cultured primary neurons using the same microscope set-up. Therefore, future studies will expand our capability to monitor γ-secretase with subcellular resolution in live mouse brains in vivo.

Reference

- Maesako M, Sekula NM, Aristarkhova A, Feschenko P, Anderson LC, Berezovska O. Visualization of PS/γ-Secretase Activity in Living Cells. iScience. 2020 Jun 26;23(6):101139. 

- Maesako M, Houser MCQ, Turchyna Y, Wolfe MS, Berezovska O. Presenilin/γ-Secretase Activity Is Located in Acidic Compartments of Live Neurons. J Neurosci. 2022 Jan 5;42(1):145-154. 

(4) Without some more validation and physiological relevant studies, it remains a single observation and rather a technical note paper, instead of a true research paper.

Please find our response above to the critique (1).  

Reviewer #2 (Public Review):

(1) Regarding the variability and spatial correlation- the dynamic range of the sensor previously reported in vitro is in the range of 20-30% change (Houser et al 2020) whereas the range of FR detected in vivo is between cells is significantly larger (Fig. 3). This raises considerable doubts for specific detection of cellular activity (see point 3).

Please find our response below to the critique (2).

(2) One direct way to test the dynamic range of the sensor in vivo, is to increase or decrease endogenous gamma-secretase activity and to ensure this experimental design allows to accurately monitor gamma-secretase activity. In the previous characterization of the reporter (Hauser et al 2020), DAPT application and inhibition of gammasecretase activity results in increased FR (Figures 2 and 3 of Houser et al). This is in agreement with the design of the biosensor, since FR should be inversely correlated with enzymatic activity. Here, while the authors repeat the same manipulation and apply DAPT to block gamma-secretase activity, it seems to induce the opposite effect and reduces FR (comparing figures 8 with figures 5,6,7). First, there is no quantification comparing FR with and without DAPT. Moreover, it is possible to conduct this experiment in the same animals, meaning comparing FR before and after DAPT in the same mouse and cell populations. This point is absolutely critical- if indeed FR is reduced following DAPT application, this needs to be explained since this contradicts the basic design and interpretation of the biosensor.

We appreciate the reviewer’s comment. In our hand, overexpression of γ-secretase four components (PSEN, Nct, Aph1, and Pen2) is the only reliable and reproducible approach to increase the cellular activity of γ-secretase, which we successfully employed in vitro but not in vivo yet. Therefore, a γ-secretase inhibitor was used to determine the dynamic range of our FRET biosensor in vivo. FRET efficiency depends on the proximity and orientation of donor and acceptor fluorescent proteins. In our initial study, we engineered the original C99 EGFP-RFP biosensor (C99 R-G), and the replacement of EGFP and RFP with mTurquoise-GL and YPet, respectively, expanded the dynamic range of the sensor approximately 2 times. Moreover, extending the linker length from 20 a.a. to 80 a.a. increased the dynamic range 2.2 times (Maesako et al., 2020 iScience). Of note, the C99 720-670 NIR analog, which has the same 80 a.a. linker but miRFP670 and miRFP720 as the donor and acceptor, exhibited a slightly better dynamic range than the C99 Y-T sensor (Houser et al., 2020 Sensor). Our interpretation, at that time, was that the cleavage of the C99 720-670 biosensor by γ-secretase results in a longer distance between the donor and acceptor, and thus, the FRET ratio always increases by γ-secretase inhibition (i.e., proximity plays a more significant role than orientation in our biosensors). As expected, a significantly increased FRET ratio was detected in various cell lines by γ-secretase inhibitors, including CHO, MEF, BV2 cells, and mouse cortical primary neurons. Moreover, to further ensure the C99 720-670 biosensor records changes in γ-secretase activity, the multiplexing capability of the biosensor was utilized. In other words, we co-expressed the C99 720-670 biosensor and visible range fluorescence reporters to record other biological events, such as changes in ion concentration, etc., in cortex primary neurons. Strikingly, several biological events uniquely detected in the neurons with diminished endogenous γ-secretase activity, i.e., neurons with higher FRET ratios, are recapitulated by pharmacological inhibition of γ-secretase (unpublished observation). This approach has allowed us to ensure that increased FRET ratios are indicative of decreased endogenous γ-secretase activity in mouse cortical primary neurons. 

However, as recommended by the reviewer, we have performed a new experiment to compare the FRET ratio before and after DAPT, a potent γ-secretase inhibitor, administration in the same mouse and cell populations. Surprisingly, we found that of DAPT significantly decreases 720/670 ratios, which is included in our revised manuscript (Figure 2—figure supplement 2C). This unexpected FRET reduction by γ-secretase inhibition was also found in mouse primary neurons derived from the cerebellum (unpublished observation). These findings suggest that orientation plays a significant role in our γ-secretase FRET biosensor and whether the FRET ratio is increased or decreased by the γ-secretase-mediated cleavage depends on cell types. Of note, the difference in FRET ratios with and without DAPT was comparable between primary cortex neurons (24.3%) and the somatosensory cortex neurons in vivo (22.1%). Our new findings suggest that how our biosensors report γ-secretase activity (i.e., increased vs. decreased FRET ratio) must be examined on a model-by-model basis, which is clearly noted in the revised manuscript: 

Reference

- Houser MC, Hou SS, Perrin F, Turchyna Y, Bacskai BJ, Berezovska O, Maesako M. A Novel NIRFRET Biosensor for Reporting PS/γ-Secretase Activity in Live Cells. Sensors (Basel). 2020 Oct 22;20(21):5980. 

- Maesako M, Sekula NM, Aristarkhova A, Feschenko P, Anderson LC, Berezovska O. Visualization of PS/γ-Secretase Activity in Living Cells. iScience. 2020 Jun 26;23(6):101139. 

(3) For further validation, I would suggest including in vivo measurements with a sensor version with no biological activity as a negative control, for example, a mutation that prevents enzymatic cleavage and FRET changes. This should be used to showcase instrumental variability and would help to validate the variability of FR is indeed biological in origin. This would significantly strengthen the claims regarding spatial correlation within population of cells.

We fully agree with the reviewer that having a sensor version containing a mutation, which prevents enzymatic cleavage and thus FRET changes, as a negative control is preferable. In our previous study, we developed and validated the APP-based C99 Y-T and Notch1-based N100 Y-T biosensors (Maesako et al., 2020 iScience). It is well established that Notch1 cleavage is entirely blocked by Notch1 V1744G mutation (Schroeter et al., 1998 Nature; Huppert et al., 2000 Nature), and therefore, we introduced the mutation into N100 Y-T biosensor and used it as a negative control. On the other hand, such a striking mutation has never been identified in APP processing. To successfully monitor γ-secretase activity in deep tissue in vivo, we replaced Turquoise-GL and YPet in the C99 Y-T and N100 Y-T biosensors with miRFP670 and miRFP720, respectively. While the APP-based C99 720-670 biosensor allows recording γ-secretase activity (Houser et al., 2020 Sensors), we found the N100 720-670 sensor exhibits a very small dynamic range, not enabling to reliably measure γ-secretase activity. Taken together, there is not currently available NIR γ-secretase biosensor with no biological activity.

Reference

- Houser MC, Hou SS, Perrin F, Turchyna Y, Bacskai BJ, Berezovska O, Maesako M. A Novel NIRFRET Biosensor for Reporting PS/γ-Secretase Activity in Live Cells. Sensors (Basel). 2020 Oct 22;20(21):5980. 

- Huppert SS, Le A, Schroeter EH, Mumm JS, Saxena MT, Milner LA, Kopan R. Embryonic lethality in mice homozygous for a processing-deficient allele of Notch1. Nature. 2000 Jun 22;405(6789):966-70. 

- Maesako M, Sekula NM, Aristarkhova A, Feschenko P, Anderson LC, Berezovska O. Visualization of PS/γ-Secretase Activity in Living Cells. iScience. 2020 Jun 26;23(6):101139. 

- Schroeter EH, Kisslinger JA, Kopan R. Notch-1 signalling requires ligand-induced proteolytic release of intracellular domain. Nature. 1998 May 28;393(6683):382-6. 

(4) In general, confocal microcopy is not ideal for in vivo imaging. Although the authors demonstrate data collected using IR imaging increases penetration depth, out of focus fluorescence is still evident (Figure 4). Many previous papers have primarily used FLIM based analysis in combination with 2p microscopy for in vivo FRET imaging (Some examples: Ma et al, Neuron, 2018; Massengil et al, Nature methods, 2022; DIaz-Garcia et al, Cell Metabolism, 2017; Laviv et al, Neuron, 2020). This technique does not rely on absolute photon number and therefore has several advantage sin terms of quantification of FRET signals in vivo.

It is therefore likely that use of previously developed sensors of gamma-secretase with conventional FRET pairs, might be better suited for in vivo imaging. This point should be at least discussed as an alternative.

The reviewer notes that 2p-FLIM may provide certain advantages over our confocal spectral imaging approach for detecting in vivo FRET. In our response below, we will address both the FRET detection method (FLIM vs. spectral) and microscope modality (2p vs. confocal). 

As noted by the reviewer, we do acknowledge that 2p-FLIM has been utilized to detect FRET in vivo. On the other hand, the ratiometric spectral FRET approach has also been utilized in many in vivo FRET studies (Kuchibhotla et al., 2008 Neuron; Kuchibhotla et al., 2014 PNAS; Hiratsuka et al., 2015 eLife; Maesako et al., 2017 eLife; Konagaya et al., 2017 Cell Rep; Calvo-Rodriguez et al., 2020 Nat Communi; Hino et al., 2022 Dev Cell). We think both approaches have advantages and disadvantages, as discussed in a previous review (Bajar et al., 2016 Sensors), but they complement each other. Indeed, we regularly employ FLIM in cell culture studies (Maesako et al., 2017 eLife; McKendell et al., 2022 Biosensors; Devkota 2024 Cell Rep), and our recent study also utilized 2p-FLIM for in vivo NIR imaging (although not for detecting FRET) (Hou et al., 2023, Nat Biomed Eng); therefore, we are confident that 2p-FLIM can be adapted in our follow-up studies for γ-secretase recording.

Regarding microscope modality, we agree with the reviewer’s point that generally two-photon microscopy can achieve larger penetration depths than confocal microscopy and is therefore more ideal for in vivo FRET imaging. However, in this study, since our aim was to quantify γ-secretase activity in the superficial layers of the cortex (<200 microns in depth), both NIR confocal and multiphoton microscopies could be used to achieve this imaging objective. Additionally, we chose to use confocal microscopy with our NIR C99 720-670 probe due to the probe’s slightly but higher sensitivity compared to our C99 Y-T probe (Houser et al., 2020 Sensors). Imaging γ-secretase activity with our NIR C99-720-670 probe has the additional advantage that it will allow us in future studies to multiplex with visible FRET pairs using multiphoton microscopy in the same brain region. Furthermore, our demonstration of in vivo FRET imaging using NIR confocal microscopy avoids some of the issues associated with multiphoton microscopy, including potential phototoxicity due to high average and peak laser powers and the high complexity and costs of the instrumentation. For future studies aimed at interrogating γ-secretase activity in deeper cortical regions, multiphoton microscopy could be applied for FLIM or ratiometric spectral imaging of either our NIR or visible FRET probes. Per the reviewer’s request, we have added multiphoton FRET imaging as an alternative in the discussion section. 

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(Recommendations For The Authors):

(5) Minor issues- Figure 4 describes the analysis procedure, which seems to be standard practice in the field. This can be described in the methods section rather than in the main figure.

Per the reviewer’s suggestion, this figure has been moved to Figure 2—figure supplement 1. 

Reviewer #3 (Public Review):

(1) This paper builds on the authors' original development of a near infrared (NIR) FRET sensor by reporting in vivo real-time measurements for gamma-secretase activity in the mouse cortex. The in vivo application of the sensor using state of the art techniques is supported by a clear description and straightforward data, and the project represents significant progress because so few biosensors work in vivo. Notably, the NIR biosensor is detectable to ~ 100 µm depth in the cortex. A minor limitation is that this sensor has a relatively modest ΔF as reported in Houser et al, which is an additional challenge for its use in vivo. Thus, the data is fully dependent on post-capture processing and computational analyses. This can unintentionally introduce biases but is not an insurmountable issue with the proper controls that the authors have performed here.

We appreciate the reviewer’s overall positive evaluation. As described in our response to the Reviewer 2’s critique (2), ΔF in vivo has been characterized (Figure 2—figure supplement 2C).

(2) The observation of gamma-secretase signaling that spreads across cells is potentially quite interesting, but it can be better supported. An alternative interpretation is that there exist pre-formed and clustered hubs of high gamma-secretase activity, and that DAPT has stochastic or differential accessibility to cells within the cluster. This could be resolved by an experiment of induction, for example, if gamma-secretase activity is induced or activated at a specific locale and there was observed coordinated spreading to neighboring neurons with their sensor.

We agree with the reviewer that the stochastic or differential accessibility of DAPT to cell clusters with different γ-secretase can be an alternative interpretation of our data, which is now included in the Discussion of the revised manuscript. Undoubtedly, the activation of γ-secretase would provide valuable information. However, as described in the response above to Reviewer 2’s critique #2, overexpressing the four components of γ-secretase (PSEN, Nct, Aph1, and Pen2) is the only reliable and reproducible approach to increasing the cellular activity of γ-secretase, which was achieved in our in vitro study but not yet in vivo. Our future study will develop and characterize the approach to induce γ-secretase activity to further perform detailed mechanistic studies.

(3) Furthermore, to rule out the possibility that uneven viral transduction was not simply responsible for the observed clustering, it would be helpful to see an analysis of 670nm fluorescence alone.

Our new analysis comparing 670 nm fluorescence intensity and that in five neighbor neurons shows a positive correlation (Figure 3—figure supplement 1A), suggesting that AAV was unevenly transduced. On the other hand, the 720/670 ratio (i.e., γ-secretase activity) is not correlated with 670 nm fluorescence intensity (i.e., C99 720-670 biosensor expression) (Figure 3—figure supplement 1B). This strongly suggests that, while C99 720-670 biosensor expression was not evenly distributed in the brain, the uneven probe expression did not impact the capability of γ-secretase recording.  

Reviewer #3 (Recommendations For The Authors):

(4) One minor suggestion might be to consider Figures 6-7 as orthogonal supporting analyses rather than "validation". It might then be helpful to present them together with Figure 5.

We have moved the initial Figure 6 and 7 to Figure 3—figure supplement 2 and Figure 4, respectively.

Author response:

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

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

My main concern is still in place. It is unclear whether the proposed method can find actual goal states, and as a result it is unclear what states it finds. Table S1 mentions the model BIOMD0000000454, which is a small metabolic pathway with known equations given in "Example One" in "Metabolic Control Analysis: Rereading Reder". In this model the goal states can be calculated analytically.

Regarding your statements below: I am not concerned that your method will be less efficient than random search (or any other search..) on small models, but I think it is important for the readers to have evidence that your method is able to discover true goal states at least in small networks, used in your study. You do show that your method scales to complex models. So, in my opinion, the missing part is to show that it is able to find true goal states.

"...For simple models whose true steady-state distribution can be derived numerically and/or analytically, it is very likely that their exploration will be much simpler and this is not where a lot of improvement over random search may be found, which explains our focus on more complex models..."

We thank you for your response and for your concerns on the lack of evidence that our method is able to re-discover the true goal states of simple models when these are known a priori. We acknowledge that adding these simple cases is useful for completeness. We did not include these simple models in our main study because in most cases a basic random search over the initial conditions will lead to the re-discovery of these goal states. For instance for the mentioned model BIOMD0000000454 described in the "Example One" from the "Metabolic Control Analysis: Rereading Reder" paper, several simplifying assumptions are made such that the system only has one steady state (x1=0.056, x2=0.769, x3=4.231) which can be found analytically as shown in the paper. In that simple case, this goal state is also straightforward to find with numerical simulation as any valid initial condition will converge to it.

To address the concerns of the reviewer, we propose to add an additional "sanity check" figure in the supplementary of the revised paper (Figure S4), as well as a “sanity check” subsection in the “Methods”, to present additional experiments made on  simple models such as this one. The novel figure and subsection can be visualized on the paper’s interactive version available online https://developmentalsystems.org/curious-exploration-of-grn-competencies, and we plan to include them as such in the further revision.  We have also included the full code to reproduce this sanity check as a ‘sanity_check.ipynb’  jupyter notebook in the github repository (https://github.com/flowersteam/curious-exploration-of-grn-competencies/blob/main/notebooks/sanity_check.ipynb).

In the novel figure S4-b, we show the results of our exploration pipeline on the suggested model BIOMD0000000454 as described in the "Example One" of the paper. These results provide evidence that the curiosity search is able to find back the correct unique goal state (x1=0.056, x2=0.769, x3=4.231), as expected.

We also include a second sanity check on BIOMD0000000341 which models the dynamics of beta-cell mass, insulin and glucose dynamics. This model has two stable fixed points representing physiological (B=300, I=10, G=100) and pathological (B=0, I=0, G=600) steady states, which are the known ground truth steady states as described in Figure 3 of the "A Model of b-Cell Mass, Insulin, and Glucose Kinetics: Pathways to Diabetes" paper. Again, as expected, curiosity search is able to find back those two steady states (Figure S4-a).

As stated in our previous answer, our main study focuses on more complex models that are not limited to one or few attractors that can easily be discovered with random initial conditions. Regarding the mentioned BIOMD0000000454, maybe something that has been confusing for the reviewer is that we indeed included it in our main study but, as specified in the caption of table S4, at the difference of what is done in the "example one" of the original paper, we let the metabolite concentrations y1,...,y5 evolve in time (instead of enforcing them as constants). When doing so, the resulting dynamics of the system are more complex and exhibit a spectrum of possible steady states (unknown a priori), which differ from the previous case with a single steady state. In that case, the new attractors are not analytically easy to find and the proposed curiosity search becomes interesting as it is able to uncover the distribution of possible steady states much more efficiently than a random search baseline, as shown in the new figures S4-c and S4-d.

We hope that these new results will address the reviewer’s concerns and provide evidence to the readers on the validity of the approach on simple networks.

eLife assessment

This important study develops a machine learning method to reveal hidden unknown functions and behavior in gene regulatory networks by searching parameter space in an efficient way. The evidence for some parts of the paper is still incomplete and needs systematic comparison to other methods and to the ground truth, but the work will be of broad interest to anyone working in biology of all stripes since the ideas reach beyond gene regulatory networks to revealing hidden functions in any complex system with many interacting parts.

We thank the editors and reviewers for their positive assessment and constructive suggestions. In our response, we acknowledge the importance of systematic comparison to other methods and to the ground truth, when available. However we also emphasize the challenges associated with evaluating such methods in the context of uncovering hidden behaviors in complex biological networks as the ground truth is often unknown. We hope that our explanations will clarify the potential of our approach in advancing the exploration of these systems.

Public Reviews:

Reviewer #1 (Public Review):

Summary: This paper suggests to apply intrinsically-motivated exploration for the discovery of robust goal states in gene regulatory networks.

Strengths:

The paper is well written. The biological motivation and the need for such methods are formulated extraordinarily well. The battery of experimental models is impressive.

We thank the reviewer for sharing interest in the research problem and for recognizing the strengths of our work.

Weaknesses:

(1) The proposed method is compared to the random search. That says little about the performance with regard to the true steady-state goal sets. The latter could be calculated at least for a few simple ODE (e.g., BIOMD0000000454, `Metabolic Control Analysis: Rereading Reder'). The experiment with 'oscillator circuits' may not be directly interpolated to the other models.

The lack of comparison to the ground truth goal set (attractors of ODE) from arbitrary initial conditions makes it hard to evaluate the true performance/contribution of the method. A part of the used models can be analyzed numerically using JAX, while there are models that can be analyzed analytically.

"...The true versatility of the GRN is unknown and can only be inferred through empirical exploration and proxy metrics....": one could perform a sensitivity analysis of the ODEs, identifying stable equilibria. That could provide a proxy for the ground truth 'versatility'.

We agree with the reviewer that one primary concern is to properly evaluate the effectiveness of the proposed method. However, as we move toward complex pathways, knowledge of the “true” steady-state goal sets is often unknown which is where the use of machine learning methods as the one we propose are particularly interesting (but challenging to evaluate).

For simple models whose true steady-state distribution can be derived numerically and/or analytically, it is very likely that their exploration will be much simpler and this is not where a lot of improvement over random search may be found, which explains our focus on more complex models. While we agree that it is still interesting to evaluate exploration methods on these simple models for checking their behavior, it is not clear how to scale this analysis to the targeted more complex systems.

For systems whose true steady state distribution cannot be derived analytically or numerically, we believe that random search is a pertinent baseline as it is commonly used in the literature to discover the attractors/trajectories of a biological network. For instance, Venkatachalapathy et al. [1] initialize stochastic simulations at multiple randomly sampled starting conditions (which is called a kinetic Monte Carlo-based method) to capture the steady states of a biological system. Similarly, Donzé et al. [29] use a Monte Carlo approach to compute the reachable set of a biological network «when the number of parameters  is large and their uncertain range  is not negligible». For the considered models, the true steady-state goal set is unknown, which is why we chose comparison with random search. We added a “Statistics” subsection in the Methods section providing additional details about the statistical analyses we perform between our method and the random search baseline.

(2) The proposed method is based on `Intrinsically Motivated Goal Exploration Processes with Automatic Curriculum Learning', which assumes state action trajectories [s_{t_0:t}, a_{t_0:t}], (2.1 Notations and Assumptions' in the IMGEP paper). However, the models used in the current work do not include external control actions, but rather only the initial conditions can be set. It is not clear from the methods whether IMGEP was adapted to this setting, and how the exploration policy was designed w/o actual time-dependent actions. What does "...generates candidate intervention parameters to achieve the current goal....", mean considering that interventions 'Sets the initial state...' as explained in Table 2?

We thank the reviewer for asking for clarification, as indeed the IMGEP methodology originates from developmental robotics scenarios which generally focus on the problem of robotic sequential decision-making, therefore assuming state action trajectories as presented in Forestier et al. [65]. However, in both cases, note that the IMGEP is responsible for sampling parameters which then govern the exploration of the dynamical system. In Forestier et al. [65], the IMGEP also only sets one vector at the start (denoted ) which was specifying parameters of a movement (like the initial state of the GRN), which was then actually produced with dynamic motion primitives which are dynamical system equations similar to GRN ODEs, so the two systems are mathematically equivalent. More generally, while in our case the “intervention” of the IMGEP (denoted ) only controls the initial state of the GRN, future work could consider more advanced sequential interventions simply by setting parameters of an action policy  at the start which could be called during the GRN’s trajectory to sample control actions  where  would be the state of the GRN. In practice this would also require setting only one vector at the start, so it would remain the same exploration algorithm and only the space of parameters would change, which illustrates the generality of the approach.

(3) Fig 2 shows the phase space for (ERK, RKIPP_RP) without mentioning the typical full scale of ERK, RKIPP_RP. It is unclear whether the path from (0, 0) to (~0.575, ~3.75) at t=1000 is significant on the typical scale of this phase space. is it significant on the typical scale of this phase space?

The purpose of Figure 2 is to illustrate an example of GRN trajectory in transcriptional space, and to illustrate what “interventions” and “perturbations” can be in that context. To that end we have used the fixed initial conditions provided in the BIOMD0000000647, replicating Figure 5 of Cho et al. [56].

While we are not sure of what the reviewer means with “typical” scale of this phase space, we would like to point reviewer toward Figure 8 which shows examples of certain paths that indeed reach further point in the same phase space (up to ~10 in RKIPP_RP levels and ~300 in ERK levels). However, while the paths displayed in Figure 8 are possible (and were discovered with the IMGEP), note that they may be “rarer” to occur naturally  in the sense that a large portion of the tested initial conditions with random search tend to converge toward smaller (ERK, RKIPP_RP) steady-state values similar to the ones displayed in Figure 2.

(4) Table 2:

a. Where is 'effective intervention' used in the method?

b. in my opinion 'controllability', 'trainability', and 'versatility' are different terms. If their correspondence is important I would suggest to extend/enhance the column "Proposed Isomorphism". otherwise, it may be confusing.

a) We thank the reviewer for pointing out that “effective intervention” is not explicitly used in the method. The idea here is that as we are exploring a complex dynamical system (here the GRN), some of the sampled interventions will be particularly effective at revealing novel unseen outcomes whereas others will fail to produce a qualitative change to the distribution of discovered outcomes. What we show in this paper, for instance in Figure 3a and Figure 4, is that the IMGEP method is particularly sample-efficient in finding those “effective interventions”, at least more than a random exploration. However we agree that the term “effective intervention” is ambiguous (does not say effective in what) and we have replaced it with “salient intervention” in the revised version.

b) We thank the reviewer for highlighting some confusing terms in our chosen vocabulary, and we have clarified those terms in the revised version. We agree that controllability/trainability and versatility are not exactly equivalent concepts, as controllability/trainability typically refers to the amount to which a system is externally controllable/trainable whereas versatility typically refers to the inherent adaptability or diversity of behaviors that a system can exhibit in response to inputs or conditions. However, they are both measuring the extent of states that can be reached by the system under a distribution of stimuli/conditions, whether natural conditions or engineered ones, which is why we believe that their correspondence is relevant.

I don't see how this table generalizes "concepts from dynamical complex systems and behavioral sciences under a common navigation task perspective".

We have replaced the verb “generalize” with “investigate” in the revised version.

Reviewer #2 (Public Review):

Summary:

Etcheverry et al. present two computational frameworks for exploring the functional capabilities of gene regulatory networks (GRNs). The first is a framework based on intrinsically-motivated exploration, here used to reveal the set of steady states achievable by a given gene regulatory network as a function of initial conditions. The second is a behaviorist framework, here used to assess the robustness of steady states to dynamical perturbations experienced along typical trajectories to those steady states. In Figs. 1-5, the authors convincingly show how these frameworks can explore and quantify the diversity of behaviors that can be displayed by GRNs. In Figs. 6-9, the authors present applications of their framework to the analysis and control of GRNs, but the support presented for their case studies is often incomplete.

Strengths:

Overall, the paper presents an important development for exploring and understanding GRNs/dynamical systems broadly, with solid evidence supporting the first half of their paper in a narratively clear way.

The behaviorist point of view for robustness is potentially of interest to a broad community, and to my knowledge introduces novel considerations for defining robustness in the GRN context.

We thank the reviewer for recognizing the strengths and novelty of the proposed experimental framework for exploring and understanding GRNs, and complex dynamical systems more generally. We agree that the results presented in the section “Possible Reuses of the Behavioral Catalog and Framework” (Fig 6-9) can be seen as incomplete along certain aspects, which we tried to make as explicit as possible throughout the paper, and why we explicitly state that these are “preliminary experiments”. Despite the discussed limitations, we believe that these experiments are still very useful to illustrate the variety of potential use-cases in which the community could benefit from such computational methods and experimental framework, and build on for future work.

Some specific weaknesses, mostly concerning incomplete analyses in the second half of the paper:

(1) The analysis presented in Fig. 6 is exciting but preliminary. Are there other appropriate methods for constructing energy landscapes from dynamical trajectories in gene regulatory networks? How do the results in this particular case study compare to other GRNs studied in the paper?

We are not aware of other methods than the one proposed by Venkatachalapathy et al. [1] for constructing an energy landscape given an input set of recorded dynamical trajectories, although it might indeed be the case. We want to emphasize that any of such methods would anyway depend on the input set of trajectories, and should therefore benefit from a set that is more representative of the diversity of behaviors that can be achieved by the GRN, which is why we believe the results presented in Figure 6 are interesting. As the IMGEP was able to find a higher diversity of reachable goal states (and corresponding trajectories) for many of the studied GRNs, we believe that similar effects should be observable when constructing the energy landscapes for these GRN models, with the discovery of additional or wider “valleys” of reachable steady states.

Additionally, it is unclear whether the analysis presented in Fig. 6C is appropriate. In particular, if the pseudopotential landscapes are constructed from statistics of visited states along trajectories to the steady state, then the trajectories derived from dynamical perturbations do not only reflect the underlying pseudo-landscape of the GRN. Instead, they also include contributions from the perturbations themselves.

We agree that the landscape displayed Fig. 6C integrates contributions from the perturbations on the GRN’s behavior, and that it can shape the landscape in various ways, for instance affecting the paths that are accessible, the shape/depth of certain valleys, etc. But we believe that qualitatively or quantitatively analyzing the effect of these perturbations  on the landscape is precisely what is interesting here: it might help 1) understand how a system respond to a range of perturbations and to visualize which behaviors are robust to those perturbations, 2) design better strategies for manipulating those systems to produce certain behaviors

(2) In Fig. 7, I'm not sure how much is possible to take away from the results as given here, as they depend sensitively on the cohort of 432 (GRN, Z) pairs used. The comparison against random networks is well-motivated. However, as the authors note, comparison between organismal categories is more difficult due to low sample size; for instance, the "plant" and "slime mold" categories each only have 1 associated GRN. Additionally, the "n/a" category is difficult to interpret.

We acknowledge that this part is speculative as stated in the paper: “the surveyed database is relatively small with respect to the wealth of available models and biological pathways, so we can hardly claim that these results represent the true distribution of competencies across these organism categories”. However, when further data is available, the same methodology can be reused and we believe that the resulting statistical analyses could be very informative to compare organismal (or other) categories.

(3) In Fig. 8, it is unclear whether the behavioral catalog generated is important to the intervention design problem of moving a system from one attractor basin to another. The authors note that evolutionary searches or SGD could also be used to solve the problem. Is the analysis somehow enabled by the behavioral catalog in a way that is complementary to those methods? If not, comparison against those methods (or others e.g. optimal control) would strengthen the paper.

We thank the reviewer for asking to clarify this point, which might not be clearly explained in the paper. Here the behavioral catalog is indeed used in a complementary way to the optimization method, by identifying a representative set of reachable attractors which are then used to define the optimization problem. For instance here, thanks to the catalog, we 1) were able to identify a “disease” region and several possible reachable states in that region and 2) use several of these states as starting points of our optimization problem, where we want to find a single intervention that can successfully and robustly reset all those points, as illustrated in Figure 8. Please note that given this problem formulation, a simple random search was used as an optimization strategy. When we mention more advanced techniques such as EA or SGD, it is to say that they might be more efficient optimizers than random search. However, we agree that in many cases optimizing directly will not work if starting from random or bad initial guess, and this even with EA or SGD. In that case the discovered behavioral catalog can be useful to better initialize  this local search and make it more efficient/useful, akin to what is done in Figure 9.

(4) The analysis presented in Fig. 9 also is preliminary. The authors note that there exist many algorithms for choosing/identifying the parameter values of a dynamical system that give rise to a desired time-series. It would be a stronger result to compare their approach to more sophisticated methods, as opposed to random search and SGD. Other options from the recent literature include Bayesian techniques, sparse nonlinear regression techniques (e.g. SINDy), and evolutionary searches. The authors note that some methods require fine-tuning in order to be successful, but even so, it would be good to know the degree of fine-tuning which is necessary compared to their method.

We agree that the analysis presented in Figure 9 is preliminary, and thank the reviewer for the suggestion. We would first like to refer to other papers from the ML literature that have more thoroughly analyzed this issue, such as Colas et al. [74] and Pugh et al. [34], and shown the interest of diversity-driven strategies as promising alternatives.  Additionally, as suggested by the reviewer, we added an additional comparison to the CMA-ES algorithm in the revised version in order to complete our analysis. CMA-ES is an evolutionary algorithm which is self-adaptive in the optimization steps and that is known to be better suited than SGD to escape local minimas when the number of parameters is not too high (here we only have 15 parameters). However, our results showed that while CMA-ES explores more the solution space at the beginning of optimization than SGD does, it also ultimately converges into a local minima similarly to SGD. The best solution converges toward a constant signal (of the target b) but fails to maintain the target oscillations, similar to the solutions discovered by gradient descent. We tried this for a few hyperparameters (init mean and std) but always found similar results.  We have updated the figure 9 image and caption, as well as descriptive text, to include these novel results in the revised version. We also added a reference to the CMA-ES paper in the citations.

Reviewer #1 (Recommendations For The Authors):

I would suggest to conduct a more rigor analysis of the performance by estimating/approximating the ground truth robust goal sets in important GRNs.

Also, the use of terminology from different disciplines can be improved. Please see my comments above. Specifically, the connection between controllability in dynamical control systems and versatility used in this paper is unclear.

We hope to have addressed the reviewer's concerns in our previous answers.

Reviewer #2 (Recommendations For The Authors):

Fig 4b: I'm not sure if DBSCAN is the appropriate method to use here, as the visual focus on the core elements of the clusters downplays the full convex hull of the points that random sampling achieves in Z space. An analysis based on convex hulls or the ball-coverage from Fig. 3b would presumably generate plots that were more similar between random sampling and curiosity search. If the goal is to highlight redundancy/non-linearity in the mapping between Z and I, another approach might be to simply bin Z-space in a grid, or to use a clustering algorithm that is less stringent about core/noise distinctions.

We thank the reviewer for the suggestion. This plot is intended to convey the reader an understanding of why a method that uniformly samples goals in Z (what the  IMGEP is doing), is more efficient than a method that uniformly samples parameters in I (what the random search is doing), in systems for which there is high redundancy/non-linearity in the mapping between I and Z. We agree that binning the Z-space in a grid and counting the number of achieved bins is a way to quantitatively measure this, which is by the way very close to what we do in Figure 3 for measuring the achieved diversity. We believe however that the clustering and coloring provides additional intuitions on why this is the case: it illustrates that large regions of the intervention space map to small regions in the outcome space and vice versa.

Additional changes in the revised version:

We added a sentence in the Methods section as well as in the caption of Table S1 providing additional details about the way we simulate the biological models from the BioModels website

We fixed a wrong reference to Figure 4 in the Methods “Sensitivity measure” subsection with reference to Figure 5.

Author response:

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

Reviewer #1 (Public Review): 

The process of EMT is a major contributor to metastasis and chemoresistance in breast cancer. By using a modified PyMT model that allows the identification of cells undergoing EMT and their decedents via S100A4-Cre mediated recombination of the mTmG allele, Ban et al. tackle a very important question of how tumor metastasis and therapy resistance by EMT can be blocked. They identified that pathways associated with ribosome biogenesis (RiBi) are activated during transition cell states. This finding represents a promising therapeutic target to block any transition from E to M (activated during cell dissemination and invasion) as well as from M to E (activated during metastatic colonization). Inhibition of RiBi-blocked EMT also reduced the establishment of chemoresistance that is associated with an EMT phenotype. Hence, RiBi blockage together with standard chemotherapy showed synergistic effects, resulting in impaired colonization/metastatic outgrowth in an animal model. The study is of great interest and of high clinical relevance as the authors show that blocking the transition from E to M or vice versa targets both aspects of metastasis, dissemination from the primary tumor, and colonization in distant organs. 

We appreciate the positive acknowledgment of our work.

The study is done with high skill using state-of-the-art technology and the conclusions are convincing and solid, but some aspects require some additional experimental support and clarification. It remains elusive whether blocking of EMT/MET is necessary for the synergistic effect of standard chemotherapy together with RiBi blockage or whether a general growth disadvantage of RiBi-treated cells independent of blocking transition is responsible. 

We appreciate the reviewer for raising the pertinent query regarding the interrelation between EMT/MET blocking by RiBi inhibition and its synergistic effect with chemotherapy drugs. Our experimental data suggests a potential consequence of these events. Specifically, when assessing the potency of RiBi inhibitors (BMH21 and CX5410), we observed a pronounced EMT/MET blocking effect at concentrations preceding the emergence of cytotoxic effects (refer to Fig. 4 and Supplementary Fig S8). Notably, the IC50 for BMH21 was approximately 200nM, which is a concentration surpassing those that manifested the EMT/MET blocking effects. Crucially, the enhanced synergy of RiBi inhibitors with chemotherapy drugs was predominantly seen at these lower concentrations (as illustrated in Supplementary Fig S10). Therefore, the EMT/MET blocking by RiBi inhibition, rather than the cytotoxic effect, is likely instrumental for the synergy with chemotherapy drugs. The result was highlighted in Page#16.

How can specific effects on state transition by RiBI block be separated from global effects attributed to overall reduced protein biosynthesis, proliferation etc.? 

We appreciate the reviewer's insightful query. We agree that RiBi activity and associated protein synthesis are fundamental processes for cell viability, making it challenging to clearly delineate the overall effects of RiBi blockage to the specific effects of EMT state transition. Our results showed an elevated RiBi activity during the EMT transitioning phases, concomitant with enhanced nascent protein synthesis, indicating a higher-than-normal requirement of new proteins for cells to switch their phenotype. This would provide us a chance to target the excessive activities of RiBi to block EMT/MET transition. Based on a similar consideration, we chose to apply shRNA instead of CRISPR technology to modulate RiBi gene expression. By comparing to scramble controls, the growth rates of the Rps knockdown cells (both RFP+ and GFP+ cells) were not significantly affected, while the EMT/MET transitioning was impaired (Supplementary Fig 9). These results may provide evidence of uncoupling the cell proliferation and EMT/MET status changes by inhibiting RiBi pathway.  

Some other aspects are misleading or need extension. 

Reviewer #1 (Recommendations For The Authors): 

(1) The analysis of RiBi expression during EMT in Fig. 1K shows that transition states have high RiBi levels, whereas E and M states are low. Analyses of MET in Fig.2G indicate that M states have the lowest, transition states upregulate RiBi while E states have the highest levels of RiBi expression. This is puzzling and how can it be explained? It would be helpful to demonstrate how these two settings are related by combining results from Figs 1 and 2 in an E-Trans-M-Trans-E state graph (in a sequence of EMT/MET). Does it mean that the initial E state starts with lower RiBi and the final E state displays the highest RiBi expression? In other words, are the initial E state and the one after MET different? 

Thank the reviewer for raising the concern about which EMT/MET state exhibits the highest RiBi activity. Following the reviewer's suggestions, we merged the scRNA-seq data of EMT and MET cells and performed the trajectory analysis. Similar epithelial-mesenchymal spectrums were detected from these cells (For reviewers Fig 1). Notably, the highest RiBi activity was detected in the early EMT transitioning or the late MET transitioning cells (revised For reviewers Fig 1D). Addressing the question of the reviewer, the initial E state (of EMT cells) did not show significant differences to the final E state (of MET cells) in comparisons of EMT pseudotime and RiBi activities. In addition, the analysis with merged cells also revealed:

(1) Both the EMT (In_Vitro_Mix) and MET (In_Vivo_GFP) cells were generally divided into two major clusters representing epithelial and mesenchymal phenotypes (For reviewers Fig 1A, 1B).

(2) The EMT and MET cells exhibited similar EMT spectrums (EMT/MET status, and pseudotime) in the trajectory analysis (For reviewers Fig 1C, 1D).

(3) Cells with high RiBi activity were mostly from the transitioning cell during EMT (In_Vitro_Mix) cells (For reviewers Fig 1D).  

(2) It needs to be elaborated on how the experiment in Fig. 4A was exactly done. Are there cells isolated directly from the autochthonous TriPyMT tumor in contrast to steady-state cultures from Fig. 1? Does the control graph represent 0d in culture or have the cells been cultured for the same amount of time as the treated samples? How do these observed 15% GFP+ cells are related to the 15% GFP+ cells obtained at day 0 and 34% at d7 control condition in Fig. 5A? 

Following the reviewer’s suggestion, we have amended the figure legend to clarify the experiment settings. In Fig. 4A, we initiated the experiment with sorted RFP+/Epcam+ cells. The control cells were cultured for the same period of time (5 days) as drug-treated cells did. We apologize for the unclear description. The percentage of GFP+ cells in this experiment is not related to the experiment in Fig 5A, where the initial cell population comprised an unsorted mix of RFP/GFP cells. 

(3) Fig. 4B: Since the bulk population is loaded in the WB, does that suggest that the epithelial state is stabilized/enhanced or does it reflect only different cell ratios? So, it would be important to show the WB for RFP+ and GFP+ cells separately. 

Thank the reviewer for the query regarding Fig. 4B. We apologize for the unclear explanation. The experimental setup for Fig 4B was identical to that of Fig 4A, where the sorted RFP+ cells were utilized at the start. Indeed, the observed increase in epithelial markers and decrease in mesenchymal markers in cells treated with BMH and CX suggest a higher proportion of cells maintaining the RFP+ state. 

Performing WB for RFP+ and GFP+ cells separately may not address the question we asked since the experiment was initialed with pure RFP+ cells. Also, the expression of the fluorescent markers is closely aligned with the EMT status of the cells with and without drug treatment.  

(4) Figs. 4-6: The authors claim that there is less EMT under treatment. If the experiment was done over 5 days (as indicated in Fig.4b legend), it is necessary to rule out that shifts in E/M ratios are attributed to the effects of treatment on proliferation/survival affecting both populations differently. How do the same cells grow under treatment when injected orthotopically/subcutaneously? 

We apologized for the unclear descriptions. The effect of blocking the transitioning of EMT with RiBi inhibitors were performed with purified RFP+/EpCam+ cells. All GFP+ cells in this experiment setting were transformed from RFP+ cells. Given the fluorescence switch was well correlated with EMT status of cells, RFP and GFP were used as EMT reporters. Similarly, we used purified GFP+/EpCam- cells as the initial population to study the MET process of tumor cells.

To address the reviewer's concern regarding how RiBi inhibition may differentially affect the growth of RFP+ and GFP+ cells, we conducted a cell cycle assay using Tri-PyMT cells, which include both RFP+ and GFP+ populations. Our results demonstrated that both RFP+ and GFP+ cells exhibited a trend towards G2/M phase accumulation when treated with BMH21. It is important to note that the impact of BMH21 on the cell cycle was less pronounced than previously reported by Fu et al. (Oncol Rep, 2017). This is likely because the dose used for EMT inhibition in our study was approximately one-tenth of the dose known to inhibit cell growth (For Reviewers Fig 2). Also, no significantly differential impacts were detected between RFP+ and GFP+ cells. 

We have previously characterized the proliferation rate of RFP+ and GFP+ populations (Lourenco et al 2020). RFP+ cells proliferate faster than GFP+ cells. Primary tumor cells derived from RFP+ cells also grew faster than GFP+ tumors (Lourenco et al 2020).

(5) Fig. 6B: this image is puzzling. Only in the lower two panels the outline of the lung is visualized by DAPI staining. The upper two panels look like there is no lung tissue in ctrl (no DAPI+GFP-RFP- cells) or show almost exclusively DAPI+GFP-RFP- cells that are present in a clustered assembly. Do the latter represent lymphoid cell clusters or normal lung tissue? 

To improve the clarity of fluorescent images in Fig 6B, we enlarged the merge images with higher contrast (Revised Fig. 6B). The DAPI+/RFP-/GFP- region represent normal lung tissue. Nodules with either RFP or GFP signals represent tumor lesions.  

(6) Text: Several typos and sentences should be revised, including p. 3 "Le et al. discovered" which should read as "Li et al. discovered", p.8 "Vimten", p.10 "Cells were then classified cells into three main categories", GSEA should be spelled out as Gene Set Enrichment Analysis (not Assay), p. 13 "cells, suggesting the impaired MET capability with upon treatment". 

We apologize for the typos. All were corrected in the revised manuscript.

(7) Figures: Color gradient indicator in Fig. 1E does not reflect the colors of the cells, Fig. S5A+C are not referenced in the text, there is mislabeling of S5B,C,D in the legend, graph in Fig. 3D is placed two times and overlapping, Fig. 6C labeling needs adjustments, labeling of Fig. 6D should be similar to Fig. 6A: CTX blue and BMH21 green. 

We apologize for these errors and made corrections. Color in Fig.1E represents the EMT status of tumor cells as indicated in the revised figure, red for more epithelial, and green for more mesenchymal features. Fig S5 is now Fig S6, and referred in the revised manuscript. Legend for figures were corrected. Labels of Fig 6 were adjusted. 

Reviewer #2 (Public Review): 

(1) The current manuscript by Ban et al describes that cells undergoing EMT have increased rRNA synthesis, as analyzed by RNA seq-based gene expression analysis, and that the increased rRNA synthesis provides a therapeutic opportunity to target chemoresistance. The cells utilized in this manuscript were isolated from the authors' Tri-PyMT EMT lineage tracing model published a few years ago which demonstrated that cells undergoing EMT are not the cells that are contributing to metastasis but rather to tumor chemoresistance (Fischer, Nature 2015). This in vivo model has since then been criticized for not capturing all relevant EMT events which the authors also acknowledge in the introduction. The authors therefore reason that they use this lineage tracing model to better understand the role of EMT in chemoresistance. 

A major problem with the current manuscript is that the authors present many of their findings as a novel without the proper acknowledgment of previously published literature in particular, Prakash et al., Nature Communications, 2019 and Dermitt, Dev Cell, 2020. In the studies by Prakash, the authors demonstrate that maintaining ongoing rRNA biogenesis is essential for the execution of the EMT program, and thus the ability of cancer cells to become migratory and invasive. Further, Prakash et al showed that blocking rRNA biogenesis with a small molecule inhibitor, CX-5461 (which is also used in the study by Ban et al) specifically inhibits breast cancer growth, invasion, EMT, and metastasis in animal models without significant toxicity to normal tissues. As such a significant revision that is necessary at this time is a rewrite of the manuscript especially the introduction and the discussion to more accurately describe and cite previously published findings and then highlight the current work by Ban et al which nicely builds on the previously published literature as it highlights the contribution of EMT to chemoresistance rather than metastasis. The suggestion for the authors is that they therefore should focus on highlighting the chemotherapy resistance angle as their Tri-PyMT EMT lineage tracing was chosen to test this angle and as such focus on both primary tumor growth and metastasis. 

We appreciate the reviewer’s insightful feedback. In response, we have revised a section in the discussion to better highlight how our study builds upon and extends the work of others. We acknowledge that the link between ribosome biogenesis (RiBi) and the epithelial-mesenchymal transition (EMT) pathway was noted by prior researches (Prakash et al. 2019; Ebright et al. 2020). In the revised manuscript, we have included extra discussion about the topic. Our findings, however, contribute to this knowledge by elucidating increased activities of RiBi during both EMT and mesenchymal-epithelial transition (MET) processes, thereby deepening our understanding of its role. Additionally, we have clarified our novel stance on EMT-targeting strategies. Rather than solely targeting the mesenchymal phenotype, we propose that inhibiting the phenotypic switching ability of tumor cells (a round trip encompassing both EMT and MET) could be more effective, as described in the introduction part.

Additional major revisions: 

(2) The authors use the FSP1-Cre Model which in the field has been questioned as to not capture all the relevant EMT events and therefore their findings should be corroborated by another EMT model system. 

We agree with the reviewer that the Fsp1-Cre model could not capture ALL the relevant EMT events. However, the fidelity and accuracy of Fsp1-Cre model in reporting EMT process of Tri-PyMT cells have also been demonstrated in our previous studies (Lourenco et al. 2020). Also, we have included additional results to further characterize this model: 1) Continuous fluorescence switching from RFP+ to GFP+ was observed in Tri-PyMT cells (Supplementary Fig S1); 2) Bulk RNA-seq data showed the differential expression of EMT marker genes with the RFP+ and GFP+ cells (Supplementary Fig S2A); 3) Single-cell RNA-seq data showed the EMT spectrum and EMT status distributions according to Fsp1(S100a4)/Epcam, and Vim/Krt18 expression (revised Supplementary Fig S3B, 3C). Hope these results clarify the reviewer’s doubt about the Fsp1-Cre model in reporting EMT of tumor cells. Of note, the evaluation of EMT status with RiBi activity does not rely solely on the fluorescent marker switch but on the ETM-related transcriptome (EMTome) of the Tri-PyMT cells. 

Again, we agree with the reviewer that the Tri-PyMT model does not report ALL relevant EMT events. In the manuscript, we have included experiments with MD-MB231-LM2 cells (Fig 6D) and analyzed the sequencing databases of breast cancer patients (revised Supplementary Fig S13, S14), to validate the findings of the association between EMT status and RiBi activity.

(3) In the current version of the manuscript, there are no measurements of rRNA synthesis, but the gene expression profiles are used as a proxy for rRNA synthesis. The authors therefore need to include measurements of rRNA synthesis corroborating the RNA sequencing data to support their scientific findings and claims. This can be accomplished by qPCR, Northern blot, or EU staining of the respective sorted cell population. Quantification of rRNA synthesis is also needed for the CX5461/BMH-21 and silencing studies. 

We agree that direct measure rRNA synthesis is important to validate the association of RiBi activity with the EMT/MET process. Following the reviewer’s suggestion, we performed EU incorporation assay with RFP+, Double+, and GFP+ Tri-PyMT cells with and without RiBi inhibitors. Under the treatment-naïve condition, the double+ (EMT-transitioning) cells exhibited highest activity of rRNA synthesis compared to either RFP+ (E) and GFP+ (M) cells (revised Supplementary Fig S7). Also, as expected, the treatment of BMH21 or CX-5461 could significantly inhibit the rRNA synthesis (revised Supplementary Fig S8B).

(4) Currently, there is no mechanistic insight as to how rRNA synthesis is increased during EMT, which would also strengthen the manuscript. This could be done through targeted ChIP analysis. 

The experimental data in the current manuscript suggest that the activation of RiBi is upstream of the EMT process, as the impaired RiBi pathway hinders the EMT of tumor cells. We are uncertain about the suggestion regarding ChIP analysis. If the reviewer refers to ChIP analysis with EMT transcription factors (i.e., Snail, Twist, and Zeb1), it may not elucidate the mechanisms by which the EMT process is associated with rRNA synthesis. Using sorted GFP/RFP double-positive Tri-PyMT cells, we found enhanced activations in the ERK and mTOR pathways in the EMT-transitioning cells (Figure 3A). It is well-documented that the ERK and mTOR pathways are key coordinators of EMT (Xie et al., Neoplasia 2004; Shin et al., PNAS 2019; Lamouille et al., J. Cell Sci. 2012; Roshan et al., Biochimie 2019). Interestingly, we also observed significantly higher phosphorylation of rpS6, a downstream indicator of mTOR pathway activation, in the Doub+ cells. As an indispensable ribosome protein, rpS6 phosphorylation could impact ribosome functions of protein translation (Bohlen et al., Nucleic Acid Res. 2021; Mieulet et al., 2007).

(5) rRNA synthesis has canonically been linked to the cell cycle therefore it will be necessary for the authors to determine the cell cycle state of their respective cell populations throughout the manuscript. 

Following the reviewer's suggestion, we analyzed the cell cycles of RFP+, GFP+, and Doub+ Tri-PyMT cells. Our analysis revealed that the proportion of proliferating RFP+ cells (in the S phase) was higher than that of proliferating GFP+ cells. Interestingly, the Doub+ cells also exhibited a higher ratio of proliferation, which was significantly greater compared to both RFP+ and GFP+ cells (revised supplementary Figure S1B).

(6) Statistics and quantifications are currently missing in several figures and need to be better explained throughout the manuscript to strengthen the scientific rigor of the studies. 

We have improved the clarity of our manuscript. Proper statistics descriptions of experiments have been carefully reviewed and adequate information was edited in the revised manuscript.

(7) Only metastasis studies are shown in the current version of the manuscript. These studies should be complemented with primary tumor studies as the main focus of the paper is the contribution of EMT to chemoresistance. 

We appreciate the reviewer's suggestion regarding the primary tumor studies. We apologize for not stating clearly in our manuscript. In response, we have revised the manuscript to outline the rationale for establishing a competitive model by injecting a mixture of RFP+ and GFP+ cells in a 1:1 ratio via the tail vein. This model is designed to study of both EMT and MET processes under chemotherapy at a distal site, where tumor cells need phenotypic switches (both EMT and MET) to adapt to and overcome chemo/environmental challenges in this context. Indeed, we have studied the primary tumor growth with the pre-EMT (RFP+) and postEMT (GFP+) cells. Their differential contribution to tumor growth was published in another paper (Lourenco etal. Cancer Res 2020). 

Reviewer #2 (Recommendations For The Authors): 

Figure 1 and associated supplementary figure panels 

Fig. 1A. More details are needed about the Tri-PyMT model and the induction of EMT in vitro. The authors mention that when growing the isolated cells they spontaneously undergo EMT when grown in 10% FBS. What is the timeline for this transition and how reproducible is it? This information is not clear from Supp. 1. When were cells taken for analysis and also how long is plasticity maintained? According to Supp 1. cell generation 15-21 seems to have a stable cell population of green, red, and yellow cells. Are these cell populations changing if one stimulates the whole cell population with a pro-EMT stimulus? Since cell proliferation is linked to rRNA synthesis the authors also need to include markers of cell cycle for the individual cell population to identify which cell cycle state each sorted cell population is associated with. 

We thank the reviewer for recommending further analysis of the cell cycle among RFP+, GFP+, and Doub+ cells. As illustrated in the revised Supplementary Figure 1B, an increased proportion of RFP+ cells was observed in the S phases in comparison to GFP+ cells. Conversely, Doub+ cells demonstrated a proliferation rate even higher than to that of RFP+ cells.

Upon sorting, RFP+ cells were found to spontaneously undergo epithelial-mesenchymal transition (EMT) when cultured in 10% FBS media, thereby converting to GFP+. We quantified the GFP+ cell percentage within the total cell population, noting a consistent transition of a certain proportion of RFP+ cells to EMT, leading to an accumulation of GFP+ cells. This accumulation stabilizes as approximately 60-70% of the entire population become GFP+. Remarkably, re-sorting RFP+ cells from this balanced tumor cell population resulted in a similar fluorescent transition pattern as observed in the parental population. The mechanisms by which tumor cells regulate the EMT phenotypes across the entire population remain unclear. Nevertheless, the equilibrium between RFP+ and GFP+ cells may be attributed in part to the more rapid proliferation of RFP+ cells and the limited proportion of tumor cells undergoing EMT.

We conducted repeated long-term cultures (up to 20 passages) of the Tri-PyMT cells, yielding consistent results. The fluorescence transition pattern in Tri-PyMT cells proved highly reliable. Further details regarding the Tri-PyMT cells have been incorporated into the Methods section.

Fig. 1B. The loading control is not even and quantification is missing, in the text, it states Vimten instead of Vimentin. 

The less loading with Doub+ cells was due to the limited number of EMT transitioning cells we could purify by flow sorting. Even though, the expression of both epithelial and mesenchymal markers in the Doub+ cells were clear. In the revised manuscript, we have quantified the Western blot results. We also apologize for the type errors and have corrected the spelling of "Vimentin."

Fig. 1K. In this figure, the authors write: 'It is worth noting that with the 2-phase classifications (Epi or Mes), the elevated RiBi activity was associated with the transitioning cells still exhibiting overall epithelial phenotypes; RiBi activities diminished as cells completed their transition to the mesenchymal phase'. But in Fig. 1K, the Ribi activity is already at a peak during the epithelial state and starts declining already at the beginning of the transition, can the authors please explain this data a bit more? The finding that ribosome biogenesis diminishes once the cells have completed their transition was shown in Prakash et al, Fig. 1 J, I, and accordingly their scientific findings should be discussed in the context of published work. 

We acknowledge the reviewer's concerns regarding the comparison of the timeline for EMT in our model with that in Prakash's study. In our model, EMT-transitioning cells are identified by their EMT marker genes and fluorescence expression. We enriched the EMT transitioning cells by sorting the Doub+ cells. Due to the RFP protein's half-life, cells remain RFP+ for 2-3 days after the reporter cassette has switched to GFP expression. In Prakash's study, the EMT transitioning phase was defines by the duration of TGF-β stimulation.

In Figure 1K, cells are categorized based on their EMT pseudotime, calculated from their expression of EMT marker genes in the EMTome. Ribosome biogenesis (RiBi) activity is highest in cells transitioning between phase 1 (Red) and phase 2 (Green), with both phases displaying predominantly epithelial phenotypes (Figures 1C, 1D, and 1E). RiBi activity declines in cells in phases 4, 5, and 3, which exhibit a mesenchymal phenotype. We have expanded the discussion to include more details in comparison with Prakash's study in the revised manuscript.

Supp Fig S4. The authors should provide a rationale for how and why the specific marker genes were selected to calculate the AUC values. 

We have chosen the specific EMT marker genes based on their overall expression levels in Tri-PyMT cells, ensuring consistency with the reported associations of their expression patterns to epithelial or mesenchymal phenotypes in the literature. We provide a detailed rationale for the selection of these genes in the Method of revised manuscript (Page #7).

Figure 2 and associated supplementary figure panel. In this figure, rRNA synthesis needs to be evaluated in the cells isolated from the lungs to corroborate the RNA sequencing findings. 

Following the reviewer’s suggestion, we performed an RT-PCR of Ribi related genes including Bop1, Gemin4, Its1, Its2, Npm1, Rpl8, Rpl29, Rps9, Rps24, Rps28, Polr1a, Setd4, Utp6, and Xpo1. Consistent with the bulk and single cell RNA sequencing, relatively higher expression of Ribi related genes were detected in Doub+ cells compared to that of RFP+ and GFP+ cells (revised Supplementary Fig S5). 

Fig 2C, as per figure Supp Fig S4 please explain the rationale for how and why the specific marker genes were selected. 

The same marker genes used for the calculation of the EMT AUC value as in Fig. 1. These marker genes were selected because their overall expression levels are readily detectable in Tri-PyMT cells, their expression patterns are consistent with their epithelial or mesenchymal phenotypes, and the associations between expression of marker genes and phenotypes are in line with the previous reports in literature. Description of AUCell value quantification was included in the revised manuscript (Page #7).

Fig. 2G. The high Ribi during the epithelial state is most likely due to the resumption of cell proliferation of these cells. The authors should check the cell cycle states of these different sets of cells. 

We agree with the reviewer that higher Ribi activity could be related to the resumption of cell proliferation of mesenchymal tumor cells. To clarify this, we revisited the scRNAseq data, and project the S phase score to the scatter plot of Ribi activity/MET pseudotime. Indeed, cells in the far mesenchymal state show low S phase score, while the proliferating cells were mostly detected in the MET transitioning phase and epithelial phase (revised Supplementary Figure S6D).

Suppl Fig. 5 Please correct the figure legends as there is no figure D. 

We apologize for the mislabeling. We have corrected the figure legend accordingly.

Figure 3. Please explain the rationale for stimulating cells with FBS for the selected time points. 

Fig. 3A. The loading control is not even, and quantification is missing. In addition, the authors should explain why the different time points were chosen and why FBS was chosen as a stimulus. In addition, from which passage of cells were these cells? 

The RFP+ Tri-PyMT cells underwent EMT and switched their expression of fluorescent marker to GFP+ when cultured with FBS. To investigate the response of cells at varying EMT statuses to an FBS-enriched environment, we isolated RFP+, Doub+, and GFP+ cells from the 4th and 5th passages of Tri-PyMT cells and probed downstream signaling pathways after FBS stimuli. The timeline for stimulation was informed by the innate activation profile of these phosphorylation-dependent signals, spanning from 10 minutes to 1 hour. We noted that ERK signaling activation in RFP+ cells occurred within minutes of FBS exposure and diminished within approximately one hour. This ERK signal was more pronounced and persisted longer in Doub+ cells. In contrast, GFP+ cells exhibited a more transient and lower ERK activation (see revised Fig 3A). To address concerns regarding potential uneven loading in our previous assays, we have now included the quantification of Western blots in the revised Fig 3A.

How and why were ERK and mTORC1 pathways chosen for analysis downstream of increased rRNA synthesis? ERK and mTORC1 have mostly been investigated in the role of cell proliferation which is why the cell cycle status of these cell populations will be important to consider in the context of their findings. 

The regulation of ribosome biogenesis (RiBi) is mediated by multiple pathways, including the myelocytomatosis oncogene (Myc), mammalian targets of rapamycin (mTOR), and noncoding RNAs, as detailed by Jiao et al. in Signal Transduction and Targeted Therapy (2023). There was no significant difference in Myc expression between tumor cells with epithelial and mesenchymal phenotypes. We thus investigated the activation of the mTOR pathway in sorted RFP+, Doub+, and GFP+ cells. Additionally, given the recognized role of the ERK/MAPK signaling pathway in regulating protein synthesis and cell proliferation, we also analyzed the activation of ERK signals. 

In alignment with the reviewer's observation regarding the potential correlation between cell proliferation rate and RiBi activation, we further characterized the cell cycle distributions of RFP+, Doub+, and GFP+ cells. Notably, the Doub+ cells exhibited a higher ratio of cells in the proliferative state (including S and G2/M phases) compared to RFP+ and GFP+ cells. Also, higher percentage of S phase cells were detected in RFP+ cells than GFP+ cells (revised Supplementary Figure S1B).

Figure 3 B, C, D. Please provide more information about which cells are analyzed in this figure. 

We apologize for the previous ambiguity regarding the cells analyzed in these figures. To clarify, the figure legend has been revised to specify that Tri-PyMT cells from the 5th to 10th passages were the subjects of analysis for cell size and nascent protein synthesis, utilizing flow cytometry.

Figure 3D. The selected images show enlarged nucleoli/ fibrillarin which is an indicator of increased rRNA synthesis however, the authors need to show an increase in rRNA transcripts by q-PCR or Northern blot and also show EU staining in these different cell states to support their claim. 

We appreciate the reviewer's recommendation to further validate the enhanced ribosome biogenesis (RiBi) in Doub+ cells. In response, we conducted RT-PCR analysis of several RiBi-related genes (revised Supplementary Fig S5). Additionally, we carried out an EU incorporation assay to illustrate the rRNA transcription activity within these cells. The new results have been incorporated into the revised manuscript (Supplementary Fig S7).

Figure 4 and associated supplementary. In this figure, the authors show that using small molecule Pol I assembly inhibitors (BMH-21 and CX-5461) reduces the expression of mesenchymal proteins. As mentioned in previous comments these results should be put in the context of published work by Prakash et al which demonstrate that upon CX-5461 and genetic silencing of Pol I EMT is hampered as demonstrated by gene expression profiles as well as functional assays. 

We revised the description of our experiments with Pol I inhibitors in the revised manuscript by including the citation context (Prakash et al Nat Commun, 2019) as mentioned above.  

Figure 4A. Please provide an explanation of how the doses of Pol I assembly inhibitors were determined and also the selected time points. The Pol I assembly inhibitors should have an effect within a few hours (Drygin, Cancer Research, 2011, Peltonen, Cancer Cell, 24). The authors also need to show that the BMH-21 and CX5461 at selected doses are indeed inhibiting rRNA synthesis in the selected cell populations. The data would also be strengthened by performing ChIP analysis demonstrating that indeed the Pol I complex is disassociated from the rDNA genes upon inhibition. 

In addition, why are there only 2 reports and how were the statistics done? Were the data normalized to the total number of cells? The graph visually shows a difference in cell numbers. Are cells dying at this concentration? More controls must be included including markers for cell stress, p53, autophagy, and apoptosis. 

The dose of Pol inhibitors was selected based on prior studies, as noted by the reviewer. Peltonen et al. demonstrated that BMH-21 inhibits growth across a wide spectrum of cancer cell lines, achieving a mean half-maximal inhibition of cell proliferation (GI50) at 160 nM (Peltonen K., et al. Cancer Cell. 2014). Consistently, in our experiments, the growth inhibitory effect of BMH-21 on Tri-PyMT cells fell within this range, at approximately 200 nM (Fig 5B, Supplementary Fig S10). 

To address the reviewer's suggestion and verify that RiBi inhibitor effectively inhibits rRNA synthesis in our study, we conducted an EU incorporation assay. This assay revealed significant inhibition of rRNA synthesis by BMH-21 and CX5461 in Tri-PyMT cells (revised Supplementary Fig S8B). Furthermore, to enhance the robustness of our findings, we repeated the BMH-21 treatment on sorted RFP+ Tri-PyMT cells across three biological replicates, which yielded consistent results.

Figure 4B. How many replicates were done for this experiment and please provide quantification as per previous comments on WB experiments. The authors should provide a rationale for why Snail and Vimentin were chosen for these studies. Also, the authors should provide a functional assay and demonstrate that cells are less migratory post-treatment and not only markers. 

Western blots with sorted Tri-PyMT cells were performed twice. We have added the quantification of these blot in the revised manuscript. Snail and Vimentin were chosen as mesenchymal markers to indicate EMT phenotype switches as those were well-studied and commonly used mesenchymal markers of EMT. The association of fluorescent marker switch and

EMT phenotype such as cell migration was well established in our previous study (Fischer et al., 2015, Lourenco et al., 2020). The morphology and migration property of GFP+ were well distinguished from RFP+ counterparts. Also, following reviewer’s suggestion, we performed migration assay with BMH21 treatment (revised Supplementary Fig 8C). Indeed, the treatment with BMH21 or CX5461 inhibited cell migration as expected.

Supplementary figure 7. The authors need to provide a rationale as to why the two Rps were chosen to inhibit ribosome biogenesis. 

The two Rps targets were chosen based on their differential expression in Doub+ cells compared with RFP+ and GFP+ cells. Also, we considered the overall expression level of these genes in Tri-PyMT cells. We have edited the according text in the revised manuscript.

Figure S7B. In the images shown there does not appear to be a significant change in the number of nucleoli however the cells seem to be smaller. This should be explained. 

We agree with the reviewer that the box plot does not clearly show the nucleoli differences between these cells. We present the data with a violin plot, which more clearly exhibit the result (revised Supplementary Fig S9B). It was also true that the sizes of the Rps knockdown cells were relatively smaller than control cells. This is consistent with the finding that the EMT transitioning cell size was bigger than the non-transitioning cells (Fig 3B)

.

Figure 5 and Supp 8. The authors should provide the background as to why the specific chemotherapeutic drugs were chosen. 

The chemotherapeutic agents employed in this study are widely used in the treatment of breast cancer. For instance, Cyclophosphamide (CTX) hampers both DNA replication and RNA transcription; Doxorubicin inhibits DNA replication by disrupting topoisomerase activity; Paclitaxel prevents cell division by stabilizing microtubules; and 5-Fluorouracil (5-FU), a pyrimidine analog, blocks thymidylate synthase, thereby disrupting DNA synthesis. Additionally, some of these agents, such as CTX and 5-FU, may directly or indirectly affect RNA polymerase, prompting us to investigate the synergistic effects of these drugs when used in combination with BMH21. We have included the information in revised manuscript. 

Fig 5B/Supp 8. Can the authors please explain why only 2 replicates were done and provide a rationale for future statistics? 

Using serial concentrations of drugs tested—6 doses for BMH21 and 8 doses for CTX—it is logical to arrange the experiment in duplicates on 96-well plates. For the statistical analysis, we conducted dose-response analysis to ascertain the IC50 values for each drug alone and in combination. Additionally, we calculated the synergy score to assess the interactions between the drugs. The methodology section of the manuscript has been enhanced to provide a clearer description of these processes in the revised version.

Figure 6. The authors should provide a rationale of why tail veins were chosen as their in vivo model system as the EMT cells do not cause metastasis and if chemoresistance is the main focus of their studies both primary and secondary tumors should be considered. Why was not the MMTVPyMT mouse model chosen where the cells were originally isolated from to test the role of the dual treatment? How was the drug concentration decided and the interval of treatments? 

We acknowledge the reviewer's concerns regarding the choice of experimental setup for our metastasis model. Certainly, utilizing the original MMTV-PyMT mice for the combination therapy experiment would be the ideal scenario. However, there are potential drawbacks to using these transgenic mice: 1) The occurrence of multiple primary tumors that develop simultaneously but without synchronized timelines (in mice aged 6-9 weeks), and the unsynchronized development of lung metastasis (from 10-16 weeks of age). This leads to uncontrollable variations in the experimental setup, particularly when establishing multiple treatment groups; 2) Gathering a sufficient number of female transgenic mice of a similar age poses another challenge; 3) The absence of tumor cell labeling complicates the focus on assays for EMT/MET phenotype changes during tumor progression. Consequently, we have chosen to employ our Tri-PyMT model for this experiment. The drug treatment protocol was established after reviewing literature on the in vivo application of CTX and BMH21 treatment (Peltonen etal. Cancer Cell 2014; Jacobs etal. JBC 2022).

Figure 6B, C. The authors should provide quantification for these data, how many mice were analyzed, and how many sections were stained and analyzed. 

We have improved the quality of these fluorescent images and clarify the methodology, including the mouse/section numbers per group, for obtaining these fluorescent images in the legend. To quantify the differential impact of BMH21 on RFP+ and GFP+ tumor cells, we performed flow cytometry (revised Supplementary Fig S11). We have also changed the presentation of these flow data to improve the clarity of these results. 

Fig 6D. How were the treatment timeline and dosing chosen? LM2 cells are derived from a metastatic site, so they are not transitioning cells they are stably mesenchymal why was this chosen as their in vivo model? 

LM2 cells were derived from the lung metastasis of MDA-MB-231 cell line. These cells exhibit predominantly mesenchymal phenotype in culture. While growing into metastasis in the lung, expressions of epithelial markers such as E-cad were upregulated (Supplementary Fig S12), suggesting a MET process may be involved the outgrowth of lung metastasis. Therefore, we choose the LM2 cells as our experimental model for assessing the effect of RiBi inhibitor on MET. The treatment timeline was determined based on previous studies of BMH21 and chemotherapy applications in vivo (Peltonen etal. Cancer Cell 2014; Jacobs etal. JBC 2022).  

Reviewer #3 (Public Review): 

Summary: 

Ban et al. investigated the role of ribosome biogenesis (RiBi) in epithelial-to-mesenchymal transition (EMT) and its contribution to chemoresistance in breast cancer. They used a Tri-PyMT EMT lineage-tracing model and scRNA-seq to analyze EMT status and found that RiBi was elevated during both EMT and mesenchymal-to-epithelial transition (MET) of cancer cells. They further revealed that nascent protein synthesis mediated by ERK and mTOR signaling pathways was essential for the completion of RiBi. Inhibiting excessive RiBi impaired EMT and MET capability. More importantly, combinatorial treatment with RiBi inhibitors and chemotherapy drugs reduced metastatic outgrowth of both epithelial and mesenchymal tumor cells. These results suggest that targeting the RiBi pathway may be an effective strategy for treating advanced breast cancer with EMT-related chemoresistance. 

Strengths: 

The conclusions of this study are generally supported by the data. However, some weaknesses still exist as mentioned below. 

Weaknesses: 

(1) The study predominantly focused on RiBi as a target for overcoming EMT-related chemoresistance. Thus, it will be necessary to provide some canonical outcomes after upregulating ribosome biogenesis, such as translation activity. I would suggest ribosome profiling or puromycin-incorporation assay, or other more suitable experiments. 

EU incorporation assay (revised Supplementary Fig S7) and puromycin incorporation assay (Fig 3C) were performed.

(2) The results were basically obtained from mice and in vitro experiments. While these results provide valuable insights, it will be valuable to validate part of the findings using some tissue samples from patients (e.g. RiBi activity) to determine the clinical relevance and potential therapeutic applications.  

We agree. We have added the analyses on the correlation between patients’ survival and RiBi activation (revised Supplementary Fig S13, S14).

(3) The results revealed that mTORC1 and ERK mediated RiBi activation. How about mTORC2? It will be informative to evaluate mTORC2 signaling. 

We investigated the role of the mTORC1 pathway in regulating RiBi activation. It is pertinent to acknowledge that the mTORC1 complex is known to positively regulate protein synthesis through the phosphorylation of ribosomal protein S6 kinase, among other mechanisms. Additionally, Rps6 is recognized as an essential component of the 40S subunit in the ribosome. We agree with the reviewer that mTORC2 may also be involved in RiBi activity, as its activation is mediated through ribosome association (Zinzalla et al., Cell 2011; Prakash et al., Nat Comm 2019). However, this association is more likely to be downstream of RiBi activation, as the RiBi inhibitor CX5461 can block the translocation of Rictor into the nucleus (Prakash et al., Nat Comm 2019).

We also revisited our sequencing data of RFP+, GFP+, and Doub+ cells. While there was no significant change in the expression of either Rptor or Rictor among these cells, the LSMean (overall expression level) of Rptor was higher than that of Rictor; for example, 163.77 vs 29.95 in RFP+ cells. This suggests that mTORC1 may play a dominant role in regulating RiBi activity in our model.

Furthermore, we analyzed how Rapamycin (an mTORC1 inhibitor) affects the EMT process in TriPyMT cells. As expected, Rapamycin-treated cells exhibited higher expression of the epithelial marker E-cadherin (Ecad) and lower expression of the mesenchymal markers Snail and Vimentin (Vim) compared to the control (For Reviewers Figure 3).

(4) The results also demonstrated promising synergic effects of Pol I inhibitor (BMH21) and chemotherapy drug (CTX) on chemo-resistant metastasis. How about using the inhibitors of mTORC1 together with CTX? 

Several mTOR inhibitors (e.g., sirolimus, temsirolimus, ridaforolimus) have demonstrated antitumor activity. The combination of mTOR inhibitors with various targeted therapies or chemotherapies is being examined in numerous clinical trials, showing promising results. Although the combination therapy of mTORC inhibitors and CTX is beyond the scope of our study, we analyzed how mTOR inhibitors may affect the EMT process in our model, as mentioned above. Western blot analysis of EMT markers (E-cadherin, Snail, and Vimentin) showed that rapamycin treatment inhibited the EMT transition of Tri-PyMT cells. (For Reviewers Figure 3).

(5) While the results demonstrate the potential efficacy of RiBi inhibitors in reducing metastatic outgrowth, other factors and mechanisms contributing to chemoresistance may exist and need further investigation. I would suggest some discussion about this aspect. 

Following reviewer’s suggestion, we have edited the discussion section with more future directions. 

Reviewer #3 (Recommendations For The Authors): 

(1) Please provide the quantified data for all western blots, rather than solely show some representative blots. 

We quantified the western blot images as shown in the revised figures. Thanks for reviewer’s suggestion.  

(2) Please add a graphic abstract or schematic to help the readers understand the whole story. 

We have summarized a schematic graph of our findings in the revised manuscript (Supplementary Fig S15).

(3) It is hard to read the numbers inside all plots of flow cytometry. 

High-resolution figures of flow plots are included in the revised manuscript.

(4) Please provide high-resolution figures for all the synergy plots.

High-resolution figures of synergy plots are included in the revised manuscript.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

In this manuscript, Wang et al. demonstrate that knockdown of DYRK1A results in reduced cell size, which is mediated by mTORC1 activity. They found that DYRK1A interacts with TSC1/TSC2 proteins which leads to the phosphorylation of TSC2 at T1462. Phosphorylation of TSC2 at T1462 inhibits TSC2 activity leading to the activation of mTORC1. The authors complement their findings by demonstrating that overexpression of RHEB (positive regulator of mTORC1) rescues the phenotype of DYRK1A (mnb in flies) mutation in the NMJ.

The authors' findings on the regulation of cell size and mTORC1 activity by DYRK1A reflect the previous findings of Levy et al. (PMID: 33840455) that cortical deletion of Dyrk1a in mice causes decreased neuronal size associated with a decreased activity of mTORC1 that can be rescued by the inhibition of Pten or supplementation of IGF1.

The authors demonstrate that T1462 phospho-site at TSC2 is phosphorylated in response to the overexpression of WT but not kinase-dead DYRK1A. However, the authors do not provide any evidence that the regulation of mTORC1 is mediated via phosphorylation of this site. In addition, T1462 site is known to be phosphorylated by Akt. There is a possibility that Akt was co-purified with TSC1/TSC2 complex and DYRK1A promotes phosphorylation of TSC2 indirectly via the activation of AKT that can be tested by using AKT depleted cells.

We thank the reviewer for reviewing this manuscript and the critical comments. Various groups have reported the significance of the Phosphorylation of TSC2 T1462, along with four other phosphorylation sites, in regulating mTORC1, and therefore, we did not deal with this in the current manuscript (Manning et al. PMID: 12150915, Inoki et al. PMID: 12172553, Zhang et al. PMID: 19593385). Regarding co-purification of AKT with TSC1/TSC2 - AKT phosphorylates T1462, S939 and S1387 (Manning et al. PMID: 12150915, Inoki et al. PMID: 12172553, Zhang et al. PMID: 19593385). However, in in vitro kinase assay, signal intensities of anti-TSC2 S939 and S1387, with or without ATP, showed no significant difference, suggesting that AKT is not pulled down with TSC1 or TSC2. DYRK1A and Kinase dead DYRK1A were expressed and purified from bacteria.  Moreover, multiple studies have purified TSC1 and TSC2 and reported no AKT co-purified (Menon et al. PMID: 24529379, Chong-kopera et al. PMID: 16464865).

RHEB is the most proximal regulator of mTORC1 and can activate mTORC1 even under amino acid starvation. The fact that RHEB overexpression rescues the cell size under DYRK1A depletion or mnb (DYRK1A in Drosophila) mutant phenotype does not prove that DYRK1A regulates the cell size via TSC1 as it would rescue any inhibitory effects upstream to mTORC1.

We agree with the reviewer that overexpression of RHEB may rescue any inhibitory effects upstream to mTORC1.  In the results and discussion sections (Page number 7, last 3 lines), we mentioned that Rheb overexpression only supports our suggestion that DYRK1A likely works upstream to RHEB. We, however, have performed another experiment to strengthen our hypothesis. We show that increased cell size phenotype due to DYRK1A overexpression can be suppressed by inhibiting the TORC1 pathway, suggesting that mTORC1 is necessary for DYRK1A-mediated cell growth.  These results are presented in Supplementary Figure 4. The results of two reciprocals of experiments (Suppression of DRYK1A/Mnb loss of function phenotypes by RHEB overexpression and suppression of rescue of DYRK1A Gain of function phenotypes) along with and regulation of TSC phosphorylation by DYRK1A strongly suggests that DYRK1A positively regulates TSC pathway.

Reviewer #2 (Public Review):

This study aims to describe a physical interaction between the kinase DYRK1A and the Tuberous Sclerosis Complex proteins (TSC1, TSC2, TBC1D7). Furthermore, this study aims to demonstrate that DYRK1A, upon interaction with the TSC proteins regulates mTORC1 activity and cell size. Additionally, this study identifies T1462 on TSC2 as a phosphorylation target of DYRK1A. Finally, the authors demonstrate the role of DYRK1A on cell size using human, mouse, and Drosophila cells.

This study, as it stands, requires further experimentation to support the conclusions on the role of DYRK1A on TSC interaction and subsequently on mTORC1 regulation. Weaknesses include, 1) The lack of an additional assessment of cell growth/size (eg. protein content, proliferation), 2) the limited data on the requirement of DYRK1A for TSC complex stability and function, and 3) the limited perturbations on the mTORC1 pathway upon DYRK1A deletion/overexpression.

We thank the reviewer for reviewing this manuscript and the comments. We have previously analyzed the effect of DYRK1A knockdown in the proliferation of THP cells (human leukemia monocytic cell line) (Li Shanshan et al. PMID: 30137413) and have shown that DYRK1A knockdown negatively affects cell proliferation. Other studies have also shown a role for DYRK1A in cell proliferation, including in foreskin fibroblasts (Chen et al. PMID: 24119401) and HepG2 cells (Frendo-Cumbo et al. PMID: 36248734). mTORC1 regulates several pathways, including protein synthesis, lipid synthesis, nucleotide synthesis, autophagy, and stress responses. We have not done the protein content as this parameter is directly affected by TORC1 activation and may not be a suitable measure for cell growth. A large number of studies involving mTORC1 regulation analyze the levels of S6K and S6 phosphorylation, as these are direct readouts of mTORC1 function   (Prentzell et al. PMID: 33497611,  Zhang et al. PMID: 17052453, Ben-Sahra et al, PMID: 23429703, Düvel et al. PMID: 20670887,  Zhang et al. PMID: 2504303). Therefore, we used these markers to assess the status of the mTORC1 pathway.

(2) ..the limited data on the requirement of DYRK1A for TSC complex stability and function,

We agree with this limitation in our study. We have not seen a significant difference in TSC1 or TSC2 protein levels in DYRK1A knockdown or overexpressing cells, so we did not follow up on this aspect.

..and 3) the limited perturbations on the mTORC1 pathway upon DYRK1A deletion /overexpression.

We have performed an additional experiment where we overexpressed DYRK1A and showed that increased cell size phenotype due to DYRK1A overexpression can be suppressed by inhibiting the TORC1 pathway, suggesting that mTORC1 is necessary for DYRK1A-mediated cell growth.  These results are presented in Supplementary Figure 4. The results of two reciprocals of experiments (Suppression of DRYK1A/Mnb loss of function phenotypes by RHEB overexpression and suppression of Rescue of DYRK1A Gain of function phenotypes) along with and regulation of TSC phosphorylation by DYRK1A suggests that DYRK1A positively regulates TSC pathway.

Finally, this study would benefit from identifying under which nutrient conditions DYRK1A interacts with the TS complex to regulate mTORC1. The interaction described here is highly impactful to the field of mTORC1-regulated cell growth and uncovers a previously unrecognized TSC-associated interacting protein. Further characterization of the role that DYRK1A plays in regulating mTORC1 activation and the upstream signals that stimulate this interaction will be extremely important for multiple diseases that exhibit mTORC1 hyper-activation.

We agree that identifying nutrients (or physiological conditions) that affect DYRK1A-mediated TSC regulation will be important to understanding the additional complexity in context-dependent mTORC1 activation/deactivation. This study has not addressed those issues, particularly due to DYRK1A's pleiotropic nature. DYRK1A has many substrates, and both overexpression and loss of DYRK1A lead to multiple phenotypes. Identifying nutrient conditions or growth factors that can regulate the activation of DYRK1A is not yet known and would require an independent investigation.

Reviewer #3 (Public Review):

The manuscript describes a combination of in vitro and in vivo results implicating Dyrk1a in the regulation of mTORC. Particular strengths of the data are this combination of cell and whole animal (drosophila) based studies. However, most of the experiments seem to lack a key additional experimental condition that could increase confidence in the authors' conclusions. Overall some tantalizing data is presented. However, there are several issues that should be clarified or otherwise addressed with additional data.

We thank the reviewer for reviewing and commenting on this manuscript.

(1) In Figure 1G, why not test overexpression levels of Dyrk1a via western rather than only looking at the RNA levels?

Induced overexpression of DYRK1A was probed by analyzing mRNA levels, as the concentration of Doxycycline used (0-100 ng/ml) did not produce enough protein that could be detected by anti-flag antibody in a western blot. We have modified the sentence (page 5, paragraph 1).

(2) In Figure 2, while there is clearly TSC1 protein in the Dyrk1a and FLAG-Dyrk1a IPs that supports an interaction between the proteins, it would be good to see the reciprocal IP experiment wherein TSC1 or TSC2 are pulled down and then the blot probed for Dyrk1a.

In the revised manuscript, we have provided evidence that TSC1 and TSC2 can interact with endogenous DYRK1A. We have performed immunoprecipitation of affinity-tagged TSC1 or TSC2 and have probed for the enrichment of DYRK1A (Supplementary Figure S2).

(3) Figures 3 A and D tested the effects of Dyrk1a knockdown using different methods in different cell lines. This is a reasonable approach to ascertain the generalizability of findings. However, each experiment is performed differently. For example, in 3A, the authors found no difference in baseline pS6, so they did a time course of treatment to induce phosphorylation and found differences depending on Dyrk1a expression. In 3D, they only show baseline effects from the CRISPR knockdown. Why not do the time course as well for consistency? Also, why the an inconsistency in approaches wherein one shows baseline effects and the other does not? The authors could also consider the pharmacologic inhibition of Dyrk1a activity as well.

We agree that different methods were used in different cell lines to assess the effect of DYRK1A. Since DYRK1A is a pleiotropic gene, its manipulation has diverse effects on different cell lines. Also, not all cell types have similar levels of mTORC activity. Hence, we had to adapt to different strategies in different cell types, which accounted for the inconsistency in the methodology.  However, various groups have used these methods to determine the activity of mTORC1 by S6 and S6K phosphorylation by both starvations, followed by the stimulation and direct estimation methods in cycling cells (Prentzell et al. PMID: 33497611,  Zhang et al. PMID: 17052453, Ben-Sahra et al, PMID: 23429703, Düvel et al. PMID: 20670887,  Zhang et al. PMID: 25043031). ShRNA-mediated knockdown in HEK293 cells does not change S6 or S6K phosphorylation levels in actively growing cells, whereas cycling NIH3T3 cells shows a significant reduction in S6 and S6K phosphorylation. As suggested, we used pharmacological inhibition of DYRK1A and 1uM Harmine to treat the HEK293 cells and perform starvation. However, cells treated and starved start to float and die in large numbers. Thus, we did not follow this experiment further.

(4) In Figure 4, RHEB overexpression increases cell size in both Dyrk1a wt and Dyrk1a shRNA treated cells, although the magnitude of the effect appears reduced in Dyrk1a shRNA cells. However, there is the possibility here that RHEB acts independently of Dyrk1a. Why not also do the experiment of Figure 1 wherein Dyrk1a is overexpressed and then knockdown RHEB in that context? If the hypothesis is supported, then RHEB knockdown should eliminate the cell size effect of Dyrk1a overexpression.

We thank the reviewer for suggesting this experiment.  We have overexpressed DYRK1A using the inducible HEK293A-Flag-DYRK1A overexpression system and treated cells with mTOR inhibitors (Rapamycin or Torin1). The results are added to the supplementary figure S4. Our results show that the increased cell size phenotype due to DYRK1A overexpression can be suppressed by inhibiting the TORC1 pathway. This suggests that mTORC1 is necessary for DYRK1A-mediated cell growth. This data further supports the hypothesis that DYRK1A is a positive regulator of the mTORC1 pathway.

(5) The discussion should incorporate relevant findings from other models, such as Arabidopsis. Barrada et al., Development (2019), 146 (3).

We have incorporated the findings from Arabidopsis (Barrada et al., Development (2019), 146 (3) PMID: 30705074) in the last paragraph of the discussion section.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) To demonstrate that DYRK1A can phosphorylate T1462 phospho-site at TSC2 in the absence of Akt using genetic and pharmacological approaches (by using pan-Akt small molecule inhibitors).

We have performed in vitro kinase assay using recombinant DYRK1A, and affinity purified TSC1/TSC2 from HEK293 cells. However, we have not been able to perform this experiment by overexpression of DYRK1A in human cells, as 1) strong overexpression of DYRK1A leads to cell cycle exit, as demonstrated by various laboratories (Soppa et al. PMID: 24806449, Hämmerle et al PMID: 21610031,  Najas et al. PMID: 26137553, Park et al. PMID: 20696760) and our observations, and 2) T1462 Antibody signal is weak and cannot be seen in cellular extracts. We have attempted this experiment with at least three different batches of T1462 antibody from CST without success.

(2) To demonstrate that endogenous phosho-mutant/mimetic substitution of T1462 phospho-site at TSC2 is sufficient to prevent the regulation of cell size/NMJ phenotype in Drosophila by DYRK1A (mnb).

This is an interesting experiment, and we thank the reviewer for this suggestion. However, we are skeptical about interpreting the possible results. Since T1462 substitution will also block the regulation by other kinases, e.g., Akt, and it may constitutively suppress the mTORC1, any interpretation will be confusing.

Reviewer #2 (Recommendations For The Authors):

(1) In section 2.1 the authors claim that DYRK1A down-regulation enhances cell growth. An additional assessment of cell growth or size would strengthen this statement. Is total protein content also increased upon DYRK1A overexpression? Does DYRK1A KD also increase cell proliferation? In Figure 1, providing the median or mean size of cells in each condition will help the reader understand the impact of DYRK1A on cell size. In Supplementary Figure 1, the important statistical differences should be highlighted.

We have not claimed that down-regulation of DYRK1A enhances cell growth. We have not tested the protein content in a cell directly. Knockdown of DYRK1A leads to a reduction in cell proliferation, as shown by various groups, including ours (Shanshan Li PMID: 30137413, Luna et al. PMID: 30343272). Cell size is a very dynamic process and is variable within the population. All the studies measuring cell size show the size using assays on a population of cells. We have not been able to figure out a way to display the median or mean cell size that accurately reflects the cell size of the whole population. 

(2) In section 2.2 the authors describe the interaction between DYRK1A and the TSC proteins. Do the DYRK1A mutants impact interaction with TSC2 and TBC1D7 or is this specific to TSC1?

We have not tested this possibility.

(3) In section 2.3, more detailed perturbations of the mTORC1 pathway are needed. Is the mTORC1 activation observed sensitive to rapamycin treatment? Since mTORC1 regulates cell size via S6 ribosomal protein and transcription via 4EBP1, phosphorylation of 4EBP1 should also be considered. In Figure 3A, what is the level of DYRK1A down-regulation? It is unclear how many shRNA constructs were used or whether these were pooled constructs or single clones. If one shRNA/sgRNA is used, it would be very helpful to validate some of the key findings of this study with at least one more clone.

Many research studies have measured the activity of various mTORC1 substrates, the most commonly used being the phosphorylation of S6 and S6K. We agree that analyzing 4EBP1 would make the study more comprehensive, but to complete the study with our limited resources and in a limited time, we have not attempted to establish the 4EBP1 phosphorylation status. We have used a previously described and validated DYRK1A shRNA (as mentioned in the methods section).

(4) In section 2.3 is T1462 an activating or inhibiting phosphorylation event? If DYRK1A phosphorylates and activates mTORC1 via RHEB, shouldn't that result in the inhibition of mTORC1?

Multiple laboratories have demonstrated that T1462 phosphorylation leads to a reduced TSC complex activity and, hence, increased mTORC1 activity (Manning et al. PMID: 12150915, Inoki, PMID: 12172553, Zhang PMID: 19593385).

(5) In section 2.4, what is the status of AKT phosphorylation? Would an AKT inhibitor be useful in this scenario?

AKT phosphorylates T1462, S939 and S1360, as demonstrated by others. However, in our in vitro assay kinase assay, the following facts suggest that AKT is not involved in T1462 phosphorylation we observed:

(1) Signal intensities of anti-TSC2 S939 and S1387 with or without ATP, do not show any significant differences, suggesting that AKT is not pulled down with TSC1 or TSC2.

(2) Multiple studies have performed phosphorylation studies of TSC1 and TSC2 and have not reported any co-purification of AKT.

(6) Very minor grammar errors were observed, mostly at the beginning of the manuscript.

We tried our best to fix grammatical errors.

Author response:

Reviewer #1 (Public Review):

In this manuscript, Yang et al. conduct a comprehensive investigation to demonstrate the role of adipose tissue Mir802 in obesity-associated inflammation and metabolic dysfunction. Using multiple models and techniques, they propose a mechanism where elevated levels of Mir802 in adipose tissue (both in mouse models and humans) trigger fat accumulation and inflammation, leading to increased adiposity and insulin resistance. They suggest that increased Mir802 levels in adipocytes during obesity result in the downregulation of TRAF3, a negative regulator of canonical and non-canonical NF-κB pathways. This downregulation induces inflammation through the production of cytokines/chemokines that attract and polarize macrophages. Concurrently, the NF-κB pathway induces the lipogenic transcriptional factor SREBP1, which promotes fat accumulation and further recruits pro-inflammatory macrophages. While the proposed model is supported by multiple experiments and consistent data, there are areas where the manuscript could be improved. Some improvements can be addressed in the text, while others require additional controls, experiments, or analyses.

1) The manuscript should provide measurements of lipid droplet/adipocyte size for all models, both in vitro and in vivo. In vivo studies should also include fat weight measurements. This is crucial to determine whether Mir802, TRAF3, and SREBP1 promote adiposity/fat accumulation across all models.

Thank you for your careful reviewing. As suggested, we have measured the size of lipid droplet and adipocyte (1J, 2A, S2I, 3F, 3L, S3L, 5I), this modification can make you and other readers understand our manuscript more clearly. In vivo studies have included fat weight measurements (Figure 2K, L; Figure 3C, D; Figure 5N). Our results determined that adipose-selective overexpression Mir802 induced adipogenesis during high fat diet induced.

2) The rationale for co-culture experiments using WAT SVF is unclear, given that Mir802 is upregulated by obesity in adipocytes, not in the stromal-vascular fraction. These experiments would be more relevant if performed using isolated adipocytes or differentiated WAT SVF.

Thank you for this important point. We are sorry for our inaccurate expression. In our study, we used differentiated WAT SVF to co-culture with primary macrophage, we illustrated it in the methods of Migration and invasion assays. We have revised it in the Flowchart of the co-culture experiments (Figure 4A). We hope that this modification will enhance readers' comprehension of our manuscript.

3) Figures 1G and 1H lack a control group (time 0 or NCD). Without this control, it is impossible to determine if inflammation precedes Mir802 upregulation.

Thank you for this insightful comment. In the previous study, we have tested the 0 weeks high fed diet treatment group of the Figures 1I and 1J, now we have added this data in the manuscript, we hope this modification can enhance our conclusion that inflammation precedes Mir802 upregulation.

4) The statement, "The knockout of Mir802 in adipose tissue did not alter food intake, body weight, glucose level, and adiposity (data not shown)," needs more detail regarding the age and sex of the animals. These data are important and should be reported, perhaps in a supplementary figure.

Thank you for your careful reviewing. To enhance our conclusions, we have added the data of food intake, body weight, glucose level, and adiposity about Mir802 KO mice treated with normal chow diet (NCD, Supplementary Figure 3E-I).

….The knockout of Mir802 in adipose tissue did not alter food intake, body weight, glucose levels, and adiposity compared with their WT littermates in both males and females when they were fed with NCD (Figure S3E-I)……

5) The terms "KO" (knockout) and "KI" (knock-in) are misleading for AAV models, as they do not modify the genome. "KD" (knockdown) and "OE" (overexpression) are more accurate.

Thank you for your good advice. We are sorry for our inaccurate expression. According to your advice, we have rewritten it. AAV models for Mir802 knockdown (Figure 3) and Traf3 overexpression (Figure 5) have changed to KD and OE respectively.

6) The statement, "Mir802 expression was unaffected in other organs (Figure S3O)," should clarify that this is except for BAT.

We appreciate the you for this insightful comment. We have clarified that Mir802 expression was unaffected in other organs except for BAT (Figure S3T, revised manuscript).

By addressing these points, the manuscript would present a more robust and clear demonstration of the role of Mir802 in obesity-associated inflammation and metabolic dysfunction.

Thanks for your positive comments. As suggested, we have modified all point.

Reviewer #2 (Public Review):

Yang et al. investigated the role of Mir802 in the development of adipose tissue (AT) inflammation during obesity. The authors found Mir802 levels are up-regulated in the AT of mouse models of obesity and insulin resistance as well as in the AT of humans. They further demonstrated that Mir802 regulates the intracellular levels of TRAF3 and downstream activation of the NF-kB pathway. Ultimately, controlling AT inflammation by manipulating Mir802 affected whole-body glucose homeostasis, highlighting the role of AT inflammatory status in whole-body metabolism. The study provides solid evidence on the role of adipocyte Mir802 in controlling inflammation and macrophage recruitment. However, how lipid mobilization from adipocytes and how engulfment of lipid droplets by macrophages control inflammatory phenotype in these cells could be better explored. The findings of this study will have a great impact in the field, contributing to the growing body of evidence on how microRNAs control the inflammatory microenvironment of AT and whole-body metabolism in obesity.

Thanks for your positive comments.

Reviewer #3 (Public Review):

Mir802 appears to accumulate before macrophage numbers increase in adipose tissue in both mice and humans. The phenotype of Mir802 overexpression and deletion in vivo is sticking and novel. Deletion of Mir802 in adipose tissue after obesity onset also attenuated Adipose inflammation and improved systemic glucose homeostasis. Understanding how Mir802 affects the crosstalk between macrophage and adipocyte is a major point. For example, does Mir802 change the inflammatory of macrophages as it increases Traf3 expression in adipocytes? This is important because macrophages are the input if inflammatory mediators that will activate the TNFR receptor signaling pathway, potentially Traf3, resulting in impaired insulin stimulated Glut4 translocation and glucose uptake. Also, modulation of Mir802 levels in vivo leads to alterations in adiposity. Here, what is a direct effect of Mir802 and what is a result of simply reduced adiposity? One point that os ket is what triggers Mir802 expression, especially in obesity.

Thanks for your important suggestions. According to your suggestions, we have addressed additional data in the revised manuscript to enhance our conclusion.

Author response:

Reviewer #1 (Public Review):

In this paper, Tompary & Davachi present work looking at how memories become integrated over time in the brain, and relating those mechanisms to responses on a priming task as a behavioral measure of memory linkage. They find that remotely but not recently formed memories are behaviorally linked and that this is associated with a change in the neural representation in mPFC. They also find that the same behavioral outcomes are associated with the increased coupling of the posterior hippocampus with category-sensitive parts of the neocortex (LOC) during a post-learning rest period-again only for remotely learned information. There was also correspondence in rest connectivity (posterior hippocampus-LOC) and representational change (mPFC) such that for remote memories specifically, the initial post-learning connectivity enhancement during rest related to longer-term mPFC representational change.

This work has many strengths. The topic of this paper is very interesting, and the data provide a really nice package in terms of providing a mechanistic account of how memories become integrated over a delay. The paper is also exceptionally well-written and a pleasure to read. There are two studies, including one large behavioral study, and the findings replicate in the smaller fMRI sample. I do however have two fairly substantive concerns about the analytic approach, where more data will be required before we can know whether the interpretations are an appropriate reflection of the findings. These and other concerns are described below.

Thank you for the positive comments! We are proud of this work, and we feel that the paper is greatly strengthened by the revisions we made in response to your feedback. Please see below for specific changes that we’ve made.

1) One major concern relates to the lack of a pre-encoding baseline scan prior to recent learning.

a) First, I think it would be helpful if the authors could clarify why there was no pre-learning rest scan dedicated to the recent condition. Was this simply a feasibility consideration, or were there theoretical reasons why this would be less "clean"? Including this information in the paper would be helpful for context. Apologies if I missed this detail in the paper.

This is a great point and something that we struggled with when developing this experiment. We considered several factors when deciding whether to include a pre-learning baseline on day two. First, the day 2 scan session was longer than that of day 1 because it included the recognition priming and explicit memory tasks, and the addition of a baseline scan would have made the length of the session longer than a typical scan session – about 2 hours in the scanner in total – and we were concerned that participant engagement would be difficult to sustain across a longer session. Second, we anticipated that the pre-learning scan would not have been a ‘clean’ measure of baseline processing, but rather would include signal related to post-learning processing of the day 1 sequences, as multi-variate reactivation of learned stimuli have been observed in rest scans collected 24-hours after learning (Schlichting & Preston, 2014). We have added these considerations to the Discussion (page 39, lines 1047-1070).

b) Second, I was hoping the authors could speak to what they think is reflected in the post-encoding "recent" scan. Is it possible that these data could also reflect the processing of the remote memories? I think, though am not positive, that the authors may be alluding to this in the penultimate paragraph of the discussion (p. 33) when noting the LOC-mPFC connectivity findings. Could there be the reinstatement of the old memories due to being back in the same experimental context and so forth? I wonder the extent to which the authors think the data from this scan can be reflected as strictly reflecting recent memories, particularly given it is relative to the pre-encoding baseline from before the remote memories, as well (and therefore in theory could reflect both the remote + recent). (I should also acknowledge that, if it is the case that the authors think there might be some remote memory processing during the recent learning session in general, a pre-learning rest scan might not have been "clean" either, in that it could have reflected some processing of the remote memories-i.e., perhaps a clean pre-learning scan for the recent learning session related to point 1a is simply not possible.)

We propose that theoretically, the post-learning recent scan could indeed reflect mixture of remote and recent sequences. This is one of the drawbacks of splitting encoding into two sessions rather than combining encoding into one session and splitting retrieval into an immediate and delayed session; any rest scans that are collected on Day 2 may have signal that relates to processing of the Day 1 remote sequences, which is why we decided against the pre-learning baseline for Day 2, as you had noted.

You are correct that we alluded to in our original submission when discussing the LOC-mPFC coupling result, and we have taken steps to discuss this more explicitly. In Brief, we find greater LOC-mPFC connectivity only after recent learning relative to the pre-learning baseline, and cortical-cortical connectivity could be indicative of processing memories that already have undergone some consolidation (Takashima et al., 2009; Smith et al., 2010). From another vantage point, the mPFC representation of Day 1 learning may have led to increased connectivity with LOC on Day 2 due to Day 1 learning beginning to resemble consolidated prior knowledge (van Kesteren et al., 2010). While this effect is consistent with prior literature and theory, it's unclear why we would find evidence of processing of the remote memories and not the recent memories. Furthermore, the change in LOC-mPFC connectivity in this scan did not correlate with memory behaviors from either learning session, which could be because signal from this scan reflects a mix of processing of the two different learning sessions. With these ideas in mind, we have fleshed out the discussion of the post-encoding ‘recent’ scan in the Discussion (page 38-39, lines 1039-1044).

c) Third, I am thinking about how both of the above issues might relate to the authors' findings, and would love to see more added to the paper to address this point. Specifically, I assume there are fluctuations in baseline connectivity profile across days within a person, such that the pre-learning connectivity on day 1 might be different from on day 2. Given that, and the lack of a pre-learning connectivity measure on day 2, it would logically follow that the measure of connectivity change from pre- to post-learning is going to be cleaner for the remote memories. In other words, could the lack of connectivity change observed for the recent scan simply be due to the lack of a within-day baseline? Given that otherwise, the post-learning rest should be the same in that it is an immediate reflection of how connectivity changes as a function of learning (depending on whether the authors think that the "recent" scan is actually reflecting "recent + remote"), it seems odd that they both don't show the same corresponding increase in connectivity-which makes me think it may be a baseline difference. I am not sure if this is what the authors are implying when they talk about how day 1 is most similar to prior investigation on p. 20, but if so it might be helpful to state that directly.

We agree that it is puzzling that we don’t see that hippocampal-LOC connectivity does not also increase after recent learning, equivalently to what we see after remote learning. However, the fact that there is an increase from baseline rest to post-recent rest in mPFC – LOC connectivity suggests that it’s not an issue with baseline, but rather that the post-recent learning scan is reflecting processing of the remote memories (although as a caveat, there is no relationship with priming).

On what is now page 23, we were referring to the notion that the Day 1 procedure (baseline rest, learning, post-learning rest) is the most straightforward replication of past work that finds a relationship between hippocampal-cortical coupling and later memory. In contrast, the Day 2 learning and rest scan are less ‘clean’ of a replication in that they are taking place in the shadow of Day 1 learning. We have clarified this in the Results (page 23, lines 597-598).

d) Fourth and very related to my point 1c, I wonder if the lack of correlations for the recent scan with behavior is interpretable, or if it might just be that this is a noisy measure due to imperfect baseline correction. Do the authors have any data or logic they might be able to provide that could speak to these points? One thing that comes to mind is seeing whether the raw post-learning connectivity values (separately for both recent and remote) show the same pattern as the different scores. However, the authors may come up with other clever ways to address this point. If not, it might be worth acknowledging this interpretive challenge in the Discussion.

We thought of three different approaches that could help us to understand whether the lack of correlations in between coupling and behavior in the recent scan was due to noise. First, we correlated recognition priming with raw hippocampal-LOC coupling separately for pre- and post-learning scans, as in Author response image 1:

Author response image 1.

Note that the post-learning chart depicts the relationship between post-remote coupling and remote priming and between post-recent coupling and recent priming (middle). Essentially, post-recent learning coupling did not relate to priming of recently learned sequences (middle; green) while there remains a trend for a relationship between post-remote coupling and priming for remotely learned sequences (middle; blue). However, the significant relationship between coupling and priming that we reported in the paper (right, blue) is driven both by the initial negative relationship that is observed in the pre-learning scan and the positive relationship in the post-remote learning scan. This highlights the importance of using a change score, as there may be spurious initial relationships between connectivity profiles and to-be-learned information that would then mask any learning- and consolidation-related changes.

We also reasoned that if comparisons between the post-recent learning scan and the baseline scan are noisier than between the post-remote learning and baseline scan, there may be differences in the variance of the change scores across participants, such that changes in coupling from baseline to post-recent rest may be more variable than coupling from baseline to post-remote rest. We conducted F-tests to compare the variance of the change in these two hippocampal-LO correlations and found no reliable difference (ratio of difference: F(22, 22) = 0.811, p = .63).

Finally, we explored whether hippocampal-LOC coupling is more stable across participants if compared across two rest scans within the same imaging session (baseline and post-remote) versus across two scans across two separate sessions (baseline and post-recent). Interestingly, coupling was not reliably correlated across scans in either case (baseline/post-remote: r = 0.03, p = 0.89 Baseline/post-recent: r = 0.07, p = .74).

Finally, we evaluated whether hippocampal-LOC coupling was correlated across different rest scans (see Author response image 2). We reasoned that if such coupling was more correlated across baseline and post-remote scans relative to baseline and post-recent scans, that would indicate a within-session stability of participants’ connectivity profiles. At the same time, less correlation of coupling across baseline and post-recent scans would be an indication of a noisier change measure as the measure would additionally include a change in individuals’ connectivity profile over time. We found that there was no difference in the correlation of hipp-LO coupling is across sessions, and the correlation was not reliably significant for either session (baseline/post-remote: r = 0.03, p = 0.89; baseline/post-recent: r = 0.07, p = .74; difference: Steiger’s t = 0.12, p = 0.9).

Author response image 2.

We have included the raw correlations with priming (page 25, lines 654-661, Supplemental Figure 6) as well as text describing the comparison of variances (page 25, lines 642-653). We did not add the comparison of hippocampal-LOC coupling across scans to the current manuscript, as an evaluation of stability of such coupling in the context of learning and reactivation seems out of scope of the current focus of the experiment, but we find this result to be worthy of follow-up in future work.

In summary, further analysis of our data did not reveal any indication that a comparison of rest connectivity across scan sessions inserted noise into the change score between baseline and post-recent learning scans. However, these analyses cannot fully rule that possibility out, and the current analyses do not provide concrete evidence that the post-recent learning scan comprises signals that are a mixture of processing of recent and remote sequences. We discuss these drawbacks in the Discussion (page 39, lines 1047-1070).

2) My second major concern is how the authors have operationalized integration and differentiation. The pattern similarity analysis uses an overall correspondence between the neural similarity and a predicted model as the main metric. In the predicted model, C items that are indirectly associated are more similar to one another than they are C items that are entirely unrelated. The authors are then looking at a change in correspondence (correlation) between the neural data and that prediction model from pre- to post-learning. However, a change in the degree of correspondence with the predicted matrix could be driven by either the unrelated items becoming less similar or the related ones becoming more similar (or both!). Since the interpretation in the paper focuses on change to indirectly related C items, it would be important to report those values directly. For instance, as evidence of differentiation, it would be important to show that there is a greater decrease in similarity for indirectly associated C items than it is for unrelated C items (or even a smaller increase) from pre to post, or that C items that are indirectly related are less similar than are unrelated C items post but not pre-learning. Performing this analysis would confirm that the pattern of results matches the authors' interpretation. This would also impact the interpretation of the subsequent analyses that involve the neural integration measures (e.g., correlation analyses like those on p. 16, which may or may not be driven by increased similarity among overlapping C pairs). I should add that given the specificity to the remote learning in mPFC versus recent in LOC and anterior hippocampus, it is clearly the case that something interesting is going on. However, I think we need more data to understand fully what that "something" is.

We recognize the importance of understanding whether model fits (and changes to them) are driven by similarity of overlapping pairs or non-overlapping pairs. We have modified all figures that visualize model fits to the neural integration model to separately show fits for pre- and post-learning (Figure 3 for mPFC, Supp. Figure 5 for LOC, Supp. Figure 9 for AB similarity in anterior hippocampus & LOC). We have additionally added supplemental figures to show the complete breakdown of similarity each region in a 2 (pre/post) x 2 (overlapping/non-overlapping sequence) x 2 (recent/remote) chart. We decided against including only these latter charts rather than the model fits since the model fits strike a good balance between information and readability. We have also modified text in various sections to focus on these new results.

In brief, the decrease in model fit for mPFC for the remote sequences was driven primarily by a decrease in similarity for the overlapping C items and not the non-overlapping ones (Supplementary Figure 3, page 18, lines 468-472).

Interestingly, in LOC, all C items grew more similar after learning, regardless of their overlap or learning session, but the increase in model fit for C items in the recent condition was driven by a larger increase in similarity for overlapping pairs relative to non-overlapping ones (Supp. Figure 5, page 21, lines 533-536).

We also visualized AB similarity in the anterior hippocampus and LOC in a similar fashion (Supplementary Figure 9).

We have also edited the Methods sections with updated details of these analyses (page 52, lines 1392-1397). We think that including these results considerably strengthen our claims and we are pleased to have them included.

3) The priming task occurred before the post-learning exposure phase and could have impacted the representations. More consideration of this in the paper would be useful. Most critically, since the priming task involves seeing the related C items back-to-back, it would be important to consider whether this experience could have conceivably impacted the neural integration indices. I believe it never would have been the case that unrelated C items were presented sequentially during the priming task, i.e., that related C items always appeared together in this task. I think again the specificity of the remote condition is key and perhaps the authors can leverage this to support their interpretation. Can the authors consider this possibility in the Discussion?

It's true that only C items from the same sequence were presented back-to-back during the priming task, and that this presentation may interfere with observations from the post-learning exposure scan that followed it. We agree that it is worth considering this caveat and have added language in the Discussion (page 40, lines 1071-1086). When designing the study, we reasoned that it was more important for the behavioral priming task to come before the exposure scans, as all items were shown only once in that task, whereas they were shown 4-5 times in a random order in the post-learning exposure phase. Because of this difference in presentation times, and because behavioral priming findings tend to be very sensitive, we concluded that it was more important to protect the priming task from the exposure scan instead of the reverse.

We reasoned, however, that the additional presentation of the C items in the recognition priming task would not substantially override the sequence learning, as C items were each presented 16 times in their sequence (ABC1 and ABC2 16 times each). Furthermore, as this reviewer suggests, the order of C items during recognition was the same for recent and remote conditions, so the fact that we find a selective change in neural representation for the remote condition and don’t also see that change for the recent condition is additional assurance that the recognition priming order did not substantially impact the representations.

4) For the priming task, based on the Figure 2A caption it seems as though every sequence contributes to both the control and primed conditions, but (I believe) this means that the control transition always happens first (and they are always back-to-back). Is this a concern? If RTs are changing over time (getting faster), it would be helpful to know whether the priming effects hold after controlling for trial numbers. I do not think this is a big issue because if it were, you would not expect to see the specificity of the remotely learned information. However, it would be helpful to know given the order of these conditions has to be fixed in their design.

This is a correct understanding of the trial orders in the recognition priming task. We chose to involve the baseline items in the control condition to boost power – this way, priming of each sequence could be tested, while only presenting each item once in this task, as repetition in the recognition phase would have further facilitated response times and potentially masked any priming effects. We agree that accounting for trial order would be useful here, so we ran a mixed-effects linear model to examine responses times both as a function of trial number and of priming condition (primed/control). While there is indeed a large effect of trial number such that participants got faster over time, the priming effect originally observed in the remote condition still holds at the same time. We now report this analysis in the Results section (page 14, lines 337-349 for Expt 1 and pages 14-15, lines 360-362 for Expt 2).

5) The authors should be cautious about the general conclusion that memories with overlapping temporal regularities become neurally integrated - given their findings in MPFC are more consistent with overall differentiation (though as noted above, I think we need more data on this to know for sure what is going on).

We realize this conclusion was overly simplistic and, in several places, have revised the general conclusions to be more specific about the nuanced similarity findings.

6) It would be worth stating a few more details and perhaps providing additional logic or justification in the main text about the pre- and post-exposure phases were set up and why. How many times each object was presented pre and post, and how the sequencing was determined (were any constraints put in place e.g., such that C1 and C2 did not appear close in time?). What was the cover task (I think this is important to the interpretation & so belongs in the main paper)? Were there considerations involving the fact that this is a different sequence of the same objects the participants would later be learning - e.g., interference, etc.?

These details can be found in the Methods section (pages 50-51, lines 1337-1353) and we’ve added a new summary of that section in the Results (page 17, lines 424- 425 and 432-435). In brief, a visual hash tag appeared on a small subset of images and participants pressed a button when this occurred, and C1 and C2 objects were presented in separate scans (as were A and B objects) to minimize inflated neural similarity due to temporal proximity.

Reviewer #2 (Public Review):

The manuscript by Tompary & Davachi presents results from two experiments, one behavior only and one fMRI plus behavior. They examine the important question of how to separate object memories (C1 and C2) that are never experienced together in time and become linked by shared predictive cues in a sequence (A followed by B followed by one of the C items). The authors developed an implicit priming task that provides a novel behavioral metric for such integration. They find significant C1-C2 priming for sequences that were learned 24h prior to the test, but not for recently learned sequences, suggesting that associative links between the two originally separate memories emerge over an extended period of consolidation. The fMRI study relates this behavioral integration effect to two neural metrics: pattern similarity changes in the medial prefrontal cortex (mPFC) as a measure of neural integration, and changes in hippocampal-LOC connectivity as a measure of post-learning consolidation. While fMRI patterns in mPFC overall show differentiation rather than integration (i.e., C1-C2 representational distances become larger), the authors find a robust correlation such that increasing pattern similarity in mPFC relates to stronger integration in the priming test, and this relationship is again specific to remote memories. Moreover, connectivity between the posterior hippocampus and LOC during post-learning rest is positively related to the behavioral integration effect as well as the mPFC neural similarity index, again specifically for remote memories. Overall, this is a coherent set of findings with interesting theoretical implications for consolidation theories, which will be of broad interest to the memory, learning, and predictive coding communities.

Strengths:

1) The implicit associative priming task designed for this study provides a promising new tool for assessing the formation of mnemonic links that influence behavior without explicit retrieval demands. The authors find an interesting dissociation between this implicit measure of memory integration and more commonly used explicit inference measures: a priming effect on the implicit task only evolved after a 24h consolidation period, while the ability to explicitly link the two critical object memories is present immediately after learning. While speculative at this point, these two measures thus appear to tap into neocortical and hippocampal learning processes, respectively, and this potential dissociation will be of interest to future studies investigating time-dependent integration processes in memory.

2) The experimental task is well designed for isolating pre- vs post-learning changes in neural similarity and connectivity, including important controls of baseline neural similarity and connectivity.

3) The main claim of a consolidation-dependent effect is supported by a coherent set of findings that relate behavioral integration to neural changes. The specificity of the effects on remote memories makes the results particularly interesting and compelling.

4) The authors are transparent about unexpected results, for example, the finding that overall similarity in mPFC is consistent with a differentiation rather than an integration model.

Thank you for the positive comments!

Weaknesses:

1) The sequence learning and recognition priming tasks are cleverly designed to isolate the effects of interest while controlling for potential order effects. However, due to the complex nature of the task, it is difficult for the reader to infer all the transition probabilities between item types and how they may influence the behavioral priming results. For example, baseline items (BL) are interspersed between repeated sequences during learning, and thus presumably can only occur before an A item or after a C item. This seems to create non-random predictive relationships such that C is often followed by BL, and BL by A items. If this relationship is reversed during the recognition priming task, where the sequence is always BL-C1-C2, this violation of expectations might slow down reaction times and deflate the baseline measure. It would be helpful if the manuscript explicitly reported transition probabilities for each relevant item type in the priming task relative to the sequence learning task and discussed how a match vs mismatch may influence the observed priming effects.

We have added a table of transition probabilities across the learning, recognition priming, and exposure scans (now Table 1, page 48). We have also included some additional description of the change in transition probabilities across different tasks in the Methods section. Specifically, if participants are indeed learning item types and rules about their order, then both the control and the primed conditions would violate that order. Since C1 and C2 items never appeared together, viewing C1 would give rise to an expectation of seeing a BL item, which would also be violated. This suggests that our priming effects are driven by sequence-specific relationships rather than learning of the probabilities of different item types. We’ve added this consideration to the Methods section (page 45, lines 1212-1221).

Another critical point to consider (and that the transition probabilities do not reflect) is that during learning, while C is followed either by A or BL, they are followed by different A or BL items. In contrast, a given A is always followed by the same B object, which is always followed by one of two C objects. While the order of item types is semi-predictable, the order of objects (specific items) themselves are not. This can be seen in the response times during learning, such that response times for A and BL items are always slower than for B and C items. We have explained this nuance in the figure text for Table 1.

2) The choice of what regions of interest to include in the different sets of analyses could be better motivated. For example, even though briefly discussed in the intro, it remains unclear why the posterior but not the anterior hippocampus is of interest for the connectivity analyses, and why the main target is LOC, not mPFC, given past results including from this group (Tompary & Davachi, 2017). Moreover, for readers not familiar with this literature, it would help if references were provided to suggest that a predictable > unpredictable contrast is well suited for functionally defining mPFC, as done in the present study.

We have clarified our reasoning for each of these choices throughout the manuscript and believe that our logic is now much more transparent. For an expanded reasoning of why we were motivated to look at posterior and not anterior hippocampus, see pages 6-7, lines 135-159, and our response to R2. In brief, past research focusing on post-encoding connectivity with the hippocampus suggests that posterior aspect is more likely to couple with category-selective cortex after learning neutral, non-rewarded objects much like the stimuli used in the present study.

We also clarify our reasoning for LOC over mPFC. While theoretically, mPFC is thought to be a candidate region for coupling with the hippocampus during consolidation, the bulk of empirical work to date has revealed post-encoding connectivity between the hippocampus and category-selective cortex in the ventral and occipital lobes (page 6, lines 123-134).

As for the use of the predictable > unpredictable contrast for functionally defining cortical regions, we reasoned that cortical regions that were sensitive to the temporal regularities generated by the sequences may be further involved in their offline consolidation and long-term storage (Danker & Anderson, 2010; Davachi & Danker, 2013; McClelland et al., 1995). We have added this justification to the Methods section (page 18, lines 454-460).

3) Relatedly, multiple comparison corrections should be applied in the fMRI integration and connectivity analyses whenever the same contrast is performed on multiple regions in an exploratory manner.

We now correct for multiple comparisons using Bonferroni correction, and this correction depends on the number of regions in which each analysis is conducted. Please see page 55, lines 1483-1490, in the Methods section for details of each analysis.

Reviewer #3 (Public Review):

The authors of this manuscript sought to illuminate a link between a behavioral measure of integration and neural markers of cortical integration associated with systems consolidation (post-encoding connectivity, change in representational neural overlap). To that aim, participants incidentally encoded sequences of objects in the fMRI scanner. Unbeknownst to participants, the first two objects of the presented ABC triplet sequences overlapped for a given pair of sequences. This allowed the authors to probe the integration of unique C objects that were never directly presented in the same sequence, but which shared the same preceding A and B objects. They encoded one set of objects on Day 1 (remote condition), another set of objects 24 hours later (recent condition) and tested implicit and explicit memory for the learned sequences on Day 2. They additionally collected baseline and post-encoding resting-state scans. As their measure of behavioral integration, the authors examined reaction time during an Old/New judgement task for C objects depending on if they were preceded by a C object from an overlapping sequence (primed condition) versus a baseline object. They found faster reaction times for the primed objects compared to the control condition for remote but not recently learned objects, suggesting that the C objects from overlapping sequences became integrated over time. They then examined pattern similarity in a priori ROIs as a measure of neural integration and found that participants showing evidence of integration of C objects from overlapping sequences in the medial prefrontal cortex for remotely learned objects also showed a stronger implicit priming effect between those C objects over time. When they examined the change in connectivity between their ROIs after encoding, they also found that connectivity between the posterior hippocampus and lateral occipital cortex correlated with larger priming effects for remotely learned objects, and that lateral occipital connectivity with the medial prefrontal cortex was related to neural integration of remote objects from overlapping sequences.

The authors aim to provide evidence of a relationship between behavioral and neural measures of integration with consolidation is interesting, important, and difficult to achieve given the longitudinal nature of studies required to answer this question. Strengths of this study include a creative behavioral task, and solid modelling approaches for fMRI data with careful control for several known confounds such as bold activation on pattern analysis results, motion, and physiological noise. The authors replicate their behavioral observations across two separate experiments, one of which included a large sample size, and found similar results that speak to the reliability of the observed behavioral phenomenon. In addition, they document several correlations between neural measures and task performance, lending functional significance to their neural findings.

Thank you for this positive assessment of our study!

However, this study is not without notable weaknesses that limit the strength of the manuscript. The authors report a behavioral priming effect suggestive of integration of remote but not recent memories, leading to the interpretation that the priming effect emerges with consolidation. However, they did not observe a reliable interaction between the priming condition and learning session (recent/remote) on reaction times, meaning that the priming effect for remote memories was not reliably greater than that observed for recent. In addition, the emergence of a priming effect for remote memories does not appear to be due to faster reaction times for primed targets over time (the condition of interest), but rather, slower reaction times for control items in the remote condition compared to recent. These issues limit the strength of the claim that the priming effect observed is due to C items of interest being integrated in a consolidation-dependent manner.

We acknowledge that the lack of a day by condition interaction in the behavioral priming effect should discussed and now discuss this data in a more nuanced manner. While it’s true that the priming effect emerges due to a slowing of the control items over time, this slowing is consistent with classic time-dependent effects demonstrating slower response times for more delayed memories. The fact that the response times in the primed condition does not show this slowing can be interpreted as a protection against this slowing that would otherwise occur. Please see page 29, lines 758-766, for this added discussion.

Similarly, the interactions between neural variables of interest and learning session needed to strongly show a significant consolidation-related effect in the brain were sometimes tenuous. There was no reliable difference in neural representational pattern analysis fit to a model of neural integration between the short and long delays in the medial prefrontal cortex or lateral occipital cortex, nor was the posterior hippocampus-lateral occipital cortex post-encoding connectivity correlation with subsequent priming significantly different for recent and remote memories. While the relationship between integration model fit in the medial prefrontal cortex and subsequent priming (which was significantly different from that occurring for recent memories) was one of the stronger findings of the paper in favor of a consolidation-related effect on behavior, is it possible that lack of a behavioral priming effect for recent memories due to possible issues with the control condition could mask a correlation between neural and behavioral integration in the recent memory condition?

While we acknowledge that lack of a statistically reliable interaction between neural measures and behavioral priming in many cases, we are heartened by the reliable difference in the relationship between mPFC similarity and priming over time, which was our main planned prediction. In addition to adding caveats in the discussion about the neural measures and behavioral findings in the recent condition (see our response to R1.1 and R1.4 for more details), we have added language throughout the manuscript noting the need to interpret these data with caution.

These limitations are especially notable when one considers that priming does not classically require a period of prolonged consolidation to occur, and prominent models of systems consolidation rather pertain to explicit memory. While the authors have provided evidence that neural integration in the medial prefrontal cortex, as well as post-encoding coupling between the lateral occipital cortex and posterior hippocampus, are related to faster reaction times for primed objects of overlapping sequences compared to their control condition, more work is needed to verify that the observed findings indeed reflect consolidation dependent integration as proposed.

We agree that more work is needed to provide converging evidence for these novel findings. However, we wish to counter the notion that systems consolidation models are relevant only for explicit memories. Although models of systems consolidation often mention transformations from episodic to semantic memory, the critical mechanisms that define the models involve changes in the neural ensembles of a memory that is initially laid down in the hippocampus and is taught to cortex over time. This transformation of neural traces is not specific to explicit/declarative forms of memory. For example, implicit statistical learning initially depends on intact hippocampal function (Schapiro et al., 2014) and improves over consolidation (Durrant et al., 2011, 2013; Kóbor et al., 2017).

Second, while there are many classical findings of priming during or immediately after learning, there are several instances of priming used to measure consolidation-related changes to newly learned information. For instance, priming has been used as a measure of lexical integration, demonstrating that new word learning benefits from a night of sleep (Wang et al., 2017; Gaskell et al., 2019) or a 1-week delay (Tamminen & Gaskell, 2013). The issue is not whether priming can occur immediately, it is whether priming increases with a delay.

Finally, it is helpful to think about models of memory systems that divide memory representations not by their explicit/implicit nature, but along other important dimensions such as their neural bases, their flexibility vs rigidity, and their capacity for rapid vs slow learning (Henke, 2010). Considering this evidence, we suggest that systems consolidation models are most useful when considering how transformations in the underlying neural memory representation affects its behavioral expression, rather than focusing on the extent that the memory representation is explicit or implicit.

With all this said, we have added text to the discussion reminding the reader that there was no statistically significant difference in priming as a function of the delay (page 29, lines 764 - 766). However, we are encouraged by the fact that the relationship between priming and mPFC neural similarity was significantly stronger for remotely learned objects relative to recently learned ones, as this is directly in line with systems consolidation theories.

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